EEG Synchronized TMS Trial for Depression: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for EEG Synchronized TMS Trial for Depression (NCT03421808), a randomized phase 2, phase 3 study. The primary outcome is Remission Rate.

2. Clinical Question

The trial tests a timing question: whether coordinating TMS pulses with the phase of an individual’s brain rhythm is associated with a different clinical remission result than delivering pulses without that synchronization. The registry’s rationale describes alpha rhythm phases as potentially relevant to the effect of stimulation and says earlier work with the combined TMS/EEG/fMRI system found different deeper-brain blood-flow changes for pulses delivered during rising and falling phases. That rationale motivates the clinical comparison; it does not establish what the remission comparison will show.

The primary outcome is a participant count meeting a threshold on the 24-item Hamilton Rating Scale for Depression. The clinical question therefore concerns remission as operationally defined in the registry, not every possible change in symptoms or brain activity. The two arms both involve TMS and EEG; the intended contrast is synchronization of the first pulse in each train. The registry record does not report a separate no-TMS arm, so the comparison addresses synchronization against non-synchronization within the described TMS regimen.

3. Trial Design

The registry describes a randomized, quadruple-masked, parallel-group trial with phases listed as Phase 2 and Phase 3. The sponsor is the Medical University of South Carolina. The record gives enrollment as 34 and status as completed. The recorded start and primary-completion dates are 2018-11-30 and 2022-01-01. Those registry entries identify the trial’s structure and administrative history; they do not explain how masking was implemented or how participants were assigned.

The two arms are named SYNC TMS and Non-Sync TMS. Both descriptions specify daily left prefrontal TMS at 120% MT, 3000 pulses per session, for 30 sessions, with EEG and delivery at the individual alpha frequency, stated as 8-12 Hz. The distinguishing feature in the arm descriptions is whether the first TMS pulse in each train of 40 pulses was synchronized. The record does not report additional procedural detail about the synchronization algorithm or how treatment delivery was checked.

The primary outcome counts participants meeting the remission definition at the fourth week of treatment, with the timeframe also allowing assessment at six weeks for participants who continued to six weeks. The reported primary arm counts have 12 participants in each arm. The registry gives overall enrollment as 34, but does not report in the registry record why the primary outcome counts differ from overall enrollment, how many participants continued to six weeks, or the analysis population definition.

Two secondary outcomes are named: the number of participants with EEG phase synchronization frequency changes, and EEG-TMS-fMRI BOLD changes in the cingulate cortex. Numerical arm results are posted for the phase-synchronization-frequency outcome. Numerical results for the cingulate-cortex BOLD outcome are not reported in the registry record. The registry record also does not report the trial’s original sample-size assumptions or a detailed statistical analysis plan.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Remission Rate, measured over At the 4th week of treatment (or 6 weeks in those who continue to 6 weeks)..

The primary endpoint is the number of participants classified as being in depression remission. Remission is defined as a score less than 10 on the 24-item Hamilton Rating Scale for Depression, whose stated range is 0 to 52; higher scores mean more severe depression. The endpoint is assessed at the fourth week of treatment, or at six weeks for participants who continue to six weeks.

A threshold-based remission outcome gives a clinically interpretable count: it records how many participants crossed the specified score boundary, rather than describing the full distribution of scores or the amount of change for each participant. A binary endpoint can be compared between arms using event counts, proportions, risk differences, or relative measures. Each approach expresses a different aspect of the same observed outcome, and none removes uncertainty when the arm counts are small.

The registry’s definition makes the endpoint reproducible in principle, but the record does not report baseline scores, individual score changes, how the assessment time was selected for participants who continued, or the handling of missing endpoint measurements. It also does not give a separate continuous symptom-score result as the primary outcome. The remission counts therefore answer a specific question about meeting a threshold at the stated assessment time, not whether average symptom scores changed, how quickly they changed, or whether brain measures changed in parallel.

7. Results Posted in the Registry

• Non-Sync TMS: 25.0% (3/12) versus 16.7% (2/12) on control; risk difference 8.3 percentage points (95% CI -24.0 to 40.7), risk ratio 1.50 (0.30–7.43); unadjusted two-proportion z-test p = 0.615.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Number of Participants With EEG Phase Synchronization Frequency Changes

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Non-Sync TMS: 8.3% (1/12) versus 25.0% (3/12) on control; risk difference -16.7 percentage points (95% CI -45.7 to 12.4), risk ratio 0.33 (0.04–2.77); unadjusted two-proportion z-test p = 0.273.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Non-Sync TMS and the control. The interval gives the range of effects that remain compatible with the data.

The registry names two secondary outcomes: participants with EEG phase synchronization frequency changes and EEG-TMS-fMRI BOLD changes in the cingulate cortex. Numerical arm results are posted for the phase-synchronization-frequency outcome. A numerical result for the cingulate-cortex BOLD outcome is not reported in the registry record. Accordingly, the secondary evidence available for interpretation is incomplete across the outcomes named in the record.

Across the primary and the numerically reported secondary outcome, the observed contrasts are not all in the same direction. The primary remission counts are numerically higher in the non-synchronized arm, while the phase-synchronization-frequency counts are numerically higher in the synchronized arm. Both comparisons are based on small arm counts, and neither provides a precise basis for broad conclusions. These measures address different questions: remission is a clinical threshold outcome, whereas the secondary measure concerns EEG phase synchronization frequency changes. A secondary physiological outcome cannot substitute for the primary clinical outcome.

Secondary findings generally carry less weight for a primary clinical conclusion because they are additional outcomes and may be exploratory. If many outcomes or analyses are tested, the chance of at least one apparently notable result can increase. Adjustment for multiplicity or a prespecified hierarchy can help address that issue, but the registry record does not report whether such procedures were planned or used. The reported secondary comparison has an unadjusted p-value, and no sponsor-reported analysis is listed for it. It should therefore be treated as exploratory rather than as confirmatory evidence.

The absence of a numerical result for the BOLD outcome also limits assessment of the full secondary pattern. It is not appropriate to infer that the outcome was null, omitted for a particular reason, or inconsistent with the other results. The record does not report those explanations. Overall, the available secondary information offers limited context around the primary comparison, but it does not remove the primary result’s uncertainty or establish a clinical effect.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Number of Participants With EEG Phase Synchronization Frequency Changes
• EEG-TMS-fMRI Bold Changes in Cingulate Cortex

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: a participant either meets the remission threshold or does not. For a binary outcome, the arm-specific event count is read alongside the number assessed. The registry posts 2 of 12 for SYNC TMS and 3 of 12 for Non-Sync TMS. Comparing proportions puts the counts on a common scale when denominators differ, while the risk difference expresses the contrast in absolute probability units. Relative risk compares the probabilities as a ratio, and the odds ratio compares the odds. These are distinct ways to describe an arm contrast, not independent findings.

What does the risk difference express?

The unadjusted risk difference is 0.083, calculated as the Non-Sync TMS remission proportion relative to the SYNC TMS proportion. A positive value means the observed proportion was higher in the non-synchronized arm; a negative value would mean it was lower. A value of zero corresponds to equal observed proportions. The 95% confidence interval, -0.240 to 0.407, includes zero and covers differences in either direction. The risk difference is often useful because it describes an absolute contrast, but its precision depends on the event counts and denominators.

How should relative measures be read?

The relative risk of 1.5 compares the observed remission probabilities, while the odds ratio of 1.667 compares the corresponding odds. The confidence intervals are 0.303 to 7.432 for the relative risk and 0.225 to 12.35 for the odds ratio. For these relative measures, a value of one represents no difference between arms. Each interval includes that reference value, and each spans a wide range. The measures therefore do not identify a precise relative contrast. Odds ratios and relative risks also do not express the same quantity, so their numeric values should not be treated as interchangeable.

What does a p-value say?

The recalculated unadjusted p-value is 0.615. A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under the assumptions of the statistical test, if that null hypothesis were true. It is not the probability that the null hypothesis is true, the probability that the observed result is due to chance, or a measure of clinical importance. A large p-value does not demonstrate equivalence or prove there is no effect. The registry’s reported chi-squared p-value is 0.6; the record does not give its effect estimate or interval.

For a count endpoint, a chi-squared test assesses whether the observed distribution across outcome categories differs between groups under its assumptions. With small event counts, results can be sensitive to the method and its assumptions. The registry names a chi-squared method for the sponsor’s analysis. A detailed explanation of the sponsor’s exact test implementation, including any small-sample adjustments, is not reported in the registry record. The recalculated result is an unadjusted analysis of the posted summary statistics, not a replacement for a more detailed analysis plan.

Why do confidence intervals matter?

A confidence interval presents a range of estimates compatible with the observed data under the method used. Its width conveys precision: a broad interval indicates that the data are consistent with a broad range of possible contrasts. The primary risk-difference interval includes no difference and contrasts in either direction, so the point estimate alone gives an incomplete account. A confidence interval is not a guarantee that the true value lies in the particular interval, nor does it account for biases or missing information that the analysis method does not address.

General statistical context: randomization can support a fair comparison when assignment and follow-up are properly implemented, but the registry record alone does not establish those implementation details. Masking can help limit some forms of expectation or assessment bias, but the record does not describe who was masked or how masking was maintained. The stated quadruple masking is a design characteristic, not a substitute for reporting allocation procedures, outcome completeness, or the analysis population.

What is the role of the recalculation?

The posted unadjusted recalculation uses arm-level counts to express the observed contrast with an effect estimate, confidence interval, and p-value. It does not adjust for baseline characteristics, account for unreported participant-level information, or recover details absent from the registry record. The record reports no discrepancy flag, so the sponsor’s own result does not conflict with the recalculation in the recorded comparison. Where an official analysis is reported, it should be distinguished from an unadjusted recalculation based on summary data.

General statistical context: over-dispersion matters when count data vary more than the assumed model allows, because standard errors can be too small and intervals too narrow if that extra variation is ignored. That issue is not a basis for asserting a problem in this binary participant-count analysis; the registry does not report an over-dispersion model or a continuous count-rate analysis. The relevant caution is the limited information in the small event counts and the absence of further analysis details.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.083, with a 95% confidence interval from -0.240 to 0.407. This range is wide relative to the point estimate and crosses zero. It is compatible with the non-synchronized arm having a lower remission proportion, little or no difference, or a higher remission proportion. The observed contrast alone therefore does not locate the underlying difference precisely.

The relative estimates tell a similar precision story. The relative risk is 1.5, with a 95% confidence interval from 0.303 to 7.432; the odds ratio is 1.667, with a 95% confidence interval from 0.225 to 12.35. Both intervals include the no-difference reference value of one and extend across a broad range. Because these measures are based on the same 2 and 3 remission events, their apparent differences in scale do not represent separate evidence.

Confidence intervals describe sampling uncertainty under the calculation method. They do not automatically include uncertainty due to missing outcomes, departures from the intended protocol, or selective reporting. The registry record does not report a missing-data method or a detailed analysis population, so precision should be interpreted in light of those omissions as well as the sparse counts. The interval is not proof that every value in its range is equally plausible, and it is not a prediction interval for a future study.

The registry’s own analysis gives p=0.6 but no interval or effect estimate. The unadjusted recalculation gives p=0.615 and makes the magnitude and direction of the estimated contrast more visible. Neither p-value resolves the broad uncertainty. In particular, lack of statistical significance should not be converted into a claim of equivalence, while the positive point estimate should not be treated as a precise finding of benefit in either arm.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. They illustrate the number of participants that would be needed under stated assumptions to detect a chosen fraction of the observed effect. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The original sample-size assumptions for this trial are not reported in the registry record, so these planning figures should not be mistaken for the trial’s own design target.

The 80% power column describes a planning scenario with an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column uses a higher planned chance of detecting that same specified effect. These are prospective planning concepts, not guarantees about a future study’s result. The figures are illustrations anchored to the observed effect, which is itself uncertain because it comes from small observed arm counts.

The rows for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect describe progressively smaller target effects. Smaller effects need more participants to detect with the same planned power and significance level. The posted estimates reflect that pattern. They should be read as planning illustrations under the stated model and assumptions, not as definitive recruitment recommendations or a reconstruction of the study’s original rationale.

This is not observed power. Observed power is not a useful substitute for reading the effect estimate and its confidence interval after results are known; the interval directly shows the uncertainty in the observed contrast.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.167; treatment proportion p₁ = 0.250; average p̄ = 0.208.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5743 = 1.1257.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5713 = 0.4808.
4. n = (1.1257 + 0.4808)² / (0.0833)² = 371.6, rounded up to 372 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.166666666666667                          # control proportion
p1 <- 0.25                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3421808)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 372 (80% power), 498 (90% power)
 75% of observed effect: n per arm = 637 (80% power), 852 (90% power)
 50% of observed effect: n per arm = 1,377 (80% power), 1,842 (90% power)
power.prop.test: 371.6 
Simulated power at n = 372 per arm: 0.803 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s analysis as a chi-squared test with p=0.6. It does not provide an effect estimate, confidence interval, or further numerical detail for that analysis. The unadjusted recalculation from the posted arm counts gives a risk difference of 0.083, a 95% confidence interval from -0.240 to 0.407, and p=0.615. The recalculation supplies an estimate and interval that help describe the size and uncertainty of the observed contrast, while the registry’s reported result remains the sponsor’s own analysis.

The record does not flag a discrepancy between these results. The two p-values are close as displayed, but they should not be treated as identical: one is the registry-reported chi-squared result, and the other is an unadjusted recalculation from summary counts. The registry record does not specify enough about the sponsor’s implementation to establish every methodological detail or explain any minor difference.

The sponsor’s p-value should not be read as evidence of equivalence, and the recalculated estimate should not be treated as a more authoritative treatment effect. Both arise from the same small set of posted outcome counts. The recalculation is descriptive and unadjusted; the sponsor’s own analysis takes precedence as the registry-reported analysis, particularly if a discrepancy were present.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary remission outcome and two secondary outcomes. When a study examines multiple outcomes or makes multiple comparisons, the probability of obtaining at least one result that appears notable by chance can increase. Statistical approaches such as family-wise error control, false-discovery procedures, or a prespecified testing hierarchy can address different aspects of multiplicity. The registry record does not report whether any such approach was planned or applied, or whether the secondary outcomes were designated as exploratory.

The sponsor-reported analysis includes a chi-squared p-value for the primary outcome. The registry lists no sponsor-reported analysis for the secondary result with numerical arm data. That secondary comparison has an unadjusted p-value. Without a reported multiplicity plan, it should not be interpreted as confirmatory evidence. The missing numerical result for the cingulate-cortex BOLD outcome further means the listed secondary outcomes cannot all be evaluated from the record.

The record provides primary outcome counts for 12 participants in each arm, while total enrollment is 34. It also gives safety denominators of 15 in SYNC TMS and 13 in Non-Sync TMS. These figures are reported for different outcomes, and the record does not explain the difference in denominators. The primary analysis population, handling of missing primary outcomes, and any imputation or sensitivity analyses are not reported in the registry record. It is therefore not possible to determine from the registry whether missing data could have affected the remission comparison.

The randomized allocation, quadruple masking, and parallel design are recorded, but details of sequence generation, allocation concealment, masking procedures, adherence, withdrawals, and protocol deviations are not reported in the registry record. The record also does not report a full prespecified statistical analysis plan, interim analyses, or the original sample-size justification. These omissions limit assessment of selective analysis, operational conduct, and the relationship between the completed enrollment and the endpoint analysis. They should be treated as reporting gaps, not as proof that a particular procedure was or was not used.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures use denominators of 15 participants at risk in SYNC TMS and 13 in Non-Sync TMS. The registry records zero serious adverse events in each group and zero deaths in each group. These are the posted serious-event counts for the reported at-risk groups; they do not show that serious events are impossible or that a broader safety profile has been established.

The record lists four other adverse events in each arm, with the same respective at-risk denominators. It does not provide the terms for those other events in the figures presented, and the list of top serious adverse event terms is empty. The registry record does not report additional details about event severity, timing, relatedness, duration, or the method used to collect events.

The safety denominators differ from the primary remission denominators of 12 per arm, and the record does not explain why. Safety counts and primary efficacy counts should therefore be read within their own reported denominators rather than assumed to describe identical analysis populations. With a small trial and limited event detail, the posted figures are descriptive and do not support broad conclusions about comparative safety.

17. What the Result Does, and Does Not, Mean

The observed primary result is a small difference in remission counts between the randomized arms: 2 participants in SYNC TMS and 3 in Non-Sync TMS, with 12 assessed in each arm. The unadjusted risk-difference estimate is 0.083 in the direction of a higher observed remission proportion in the non-synchronized arm. Its confidence interval ranges from -0.240 to 0.407, so the data are compatible with differences in either direction as well as little difference.

The result does not establish that synchronized TMS is superior, that non-synchronized TMS is superior, or that the approaches are equivalent. The registry’s chi-squared p-value is 0.6, and the unadjusted recalculation gives p=0.615. Neither p-value answers the equivalence question. The confidence interval’s width emphasizes that the posted counts do not estimate the contrast precisely.

The trial’s rationale concerns whether timing stimulation with the brain’s EEG phase may affect stimulation effects, including potential deeper-brain responses. The remission endpoint addresses a clinical threshold, while the secondary outcomes include EEG phase synchronization frequency changes and cingulate-cortex BOLD changes. The record does not provide numerical BOLD results, so the full set of proposed physiological outcomes cannot be assessed from the posted information. Nor can a secondary signal be assumed to explain or predict the remission counts.

The findings describe this trial’s recorded participants, treatment comparison, endpoint definition, and assessment timeframe. They do not show how the intervention compares with no TMS, because both recorded arms receive TMS. The registry record also does not provide the detailed analysis population, missing-data handling, or original sample-size plan needed to assess those aspects. Any broader interpretation should account for the imprecision, the limited number of primary events, the missing reporting details, and the distinction between a mechanistic rationale and a demonstrated clinical result.

18. Why This Trial Matters Statistically

This trial raises a statistical question that is more specific than whether TMS is associated with a clinical outcome: does synchronizing stimulation to EEG phase add information or alter the observed outcome compared with non-synchronized stimulation? A randomized parallel comparison is relevant to that contrast because both arms receive TMS and the intended difference is synchronization. The registry describes quadruple masking, although the procedures used to implement it are not reported in the registry record.

The outcome choice also matters. Remission turns a symptom scale into a participant-level event, making the comparison intuitive as counts and proportions. But thresholding a continuous score discards information about how far participants are from the threshold and how their scores change over time. The posted remission counts answer the stated threshold question; they do not describe the full score distribution or the physiological pathway proposed in the rationale.

The example illustrates why effect estimates and confidence intervals matter alongside p-values. The risk-difference estimate gives the observed direction and magnitude on an absolute scale, while its broad interval conveys that these data allow substantial uncertainty. A non-significant p-value does not establish sameness, and a positive point estimate does not establish a reliable difference. The relative estimates also remain imprecise.

The trial is also a useful reminder that enrollment, endpoint denominators, and safety denominators are not automatically interchangeable. The record reports total enrollment of 34, primary counts of 12 per arm, and different safety at-risk counts. Without an explanation of these populations and missing outcomes, readers cannot fully reconstruct who contributed to each analysis. Statistical interpretation depends not only on calculations but also on transparent reporting of the populations and procedures behind them.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary comparison is based on 2 and 3 remission events, with 12 participants in each arm. The resulting confidence intervals are broad, limiting precision. The registry reports overall enrollment of 34 but does not explain why the primary outcome counts cover fewer participants or specify the primary analysis population. Missing outcome handling and sensitivity analyses are not reported in the registry record.

The endpoint timeframe allows assessment at the fourth week or, for participants who continue, at six weeks. The record does not explain how the applicable assessment time was determined, how many participants continued to six weeks, or whether the groups had comparable assessment timing. This complicates interpretation of the endpoint as a single fixed-time comparison.

The registry lists two secondary outcomes but provides a numerical result for only the EEG phase synchronization frequency outcome. A numerical result for the cingulate-cortex BOLD outcome is not reported in the registry record. The record does not report whether multiplicity was addressed, whether secondary outcomes were prespecified as confirmatory, or how missing secondary results were handled.

The trial’s original sample-size assumptions, detailed statistical analysis plan, interim analyses, allocation procedures, and masking implementation are not reported in the registry record. The posted planning figures are illustrations based on the observed effect, not the original study design. Safety counts use denominators different from the primary efficacy counts, and the reason is not explained. These limitations restrict how far the posted estimates can be generalized or used to assess conduct and reporting; they do not by themselves establish bias or protocol deviations.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: EEG Synchronized TMS Trial for Depression — NCT03421808.
• Registry record last updated 2025-11-04; status last verified 2025-10.
• Results first posted 2025-08-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes NCT03421808 as a completed randomized, quadruple-masked, parallel-group trial, with phases listed as Phase 2 and Phase 3 and enrollment of 34. It compares daily EEG-synchronized with non-synchronized left prefrontal TMS in depression. Both arm descriptions give 120% MT, 3000 pulses per session, and 30 sessions.

The primary outcome is remission, defined as a score less than 10 on the 24-item Hamilton Rating Scale for Depression, assessed at the fourth week or at six weeks for participants who continued. The posted counts are 2 of 12 in SYNC TMS and 3 of 12 in Non-Sync TMS. The unadjusted risk difference is 0.083, with a 95% confidence interval from -0.240 to 0.407; the recalculated p-value is 0.615. The registry-reported chi-squared p-value is 0.6.

The available estimates are imprecise and do not establish a difference or equivalence. One secondary outcome has numerical results; the cingulate-cortex BOLD result is not reported in the registry record. The record does not report the original sample-size assumptions, missing-data method, or detailed statistical analysis plan.