The Safety and Efficacy of Nexalin Trans-cranial Electrical Stimulation Stimulation for the Treatment of Depression: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Safety and Efficacy of Nexalin Trans-cranial Electrical Stimulation Stimulation for the Treatment of Depression (NCT03277846), a randomized na study. The primary outcome is Treatment Response.

2. Clinical Question

3. Trial Design

The registry identifies this as a randomized, parallel-group study with quadruple masking. Its official title describes a randomized, double-blind, placebo-controlled, parallel-group study among patients referred to ECT, while the structured masking entry says quadruple. Both descriptions are part of the record; further details about who was masked and how masking was implemented are not reported in the registry record.

The study enrolled 101 participants and is marked completed. Its recorded start date is 2017-09-01, and its primary completion date is 2018-05-17. The phase is listed as NA. The sponsor is the University of Pennsylvania. The intervention listed is Nexalin-based transcranial electrical stimulation, and the posted comparison is TES versus TES-SHAM.

The study description initially included an ECT arm and described a secondary aim of assessing whether Nexalin might be used as an alternative to ECT. The post-study note says the ECT arm, which was intended to profile participants as ECT accepters or rejecters, was dropped owing to site objections from referring clinicians. The note says the study was then framed as a simple comparison of TES with sham TES. Therefore, the posted primary comparison is not a direct comparison of TES with ECT.

The primary outcome data cover 78 participants: 38 in the TES group and 40 in the sham group. The registry explains that these participants met a minimum duration and treatment threshold and provided the full complement of data. The reasons that other enrolled participants did not appear in these outcome counts, and the groups or procedures used to assess them, are not reported in the registry record. The posted safety group denominators are different from the primary outcome denominators, so the safety counts should be read as a separate set of registry summaries rather than as the outcome analysis population.

The registry records one outcome measure and no secondary outcomes. It reports a comparison for the primary outcome, but detailed protocol information about allocation procedures, masking procedures, or a prespecified statistical analysis plan is not reported in the registry record.

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:

Analysis population for the primary outcome, as defined in the registry: 101 were enrolled. 78 subjects were in study for the minimum time / minimum number of treatments and provided the full compliment of data.

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 Treatment Response, measured over 1-2 weeks.

The primary endpoint is treatment response, counted as participants. The registry defines response as a 50% reduction or a score below 10 on the PHQ-9. It describes the PHQ-9 as a 9-item scale, with each item ranging from 0 to 3 and the scale ranging from 0-27. The registry says percent change from admission to “ex-take” was used as the metric, and gives a timeframe of 1-2 weeks.

A responder count turns each participant’s outcome into a binary classification: meeting or not meeting the stated response criterion. Comparing the number who respond in each group can describe how often the defined outcome occurred under TES and sham TES. It is a different summary from comparing average PHQ-9 scores, and does not retain the full range of scores or changes for every participant. The registry does not report the individual score distributions or a separate continuous-score result.

The primary outcome group counts are 28 responders among 38 participants assigned to TES and 29 among 40 assigned to TES-SHAM. These are the posted outcome denominators, and the registry says 78 participants met the minimum time and treatment requirements and posted the full complement of outcome data. The precise operational meaning of “ex-take,” including the exact assessment timing within the 1-2 weeks, is not reported in the registry record. The endpoint is therefore interpreted according to the definition and timing as recorded, without assuming further assessment procedures.

7. Results Posted in the Registry

• Transcranial Electrical Stimulation: 73.7% (28/38) versus 72.5% (29/40) on control; risk difference 1.2 percentage points (95% CI -18.5 to 20.9), risk ratio 1.02 (0.78–1.33); unadjusted two-proportion z-test p = 0.906.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant is counted as a responder or not a responder using the registry’s response definition. For such an outcome, a group proportion describes the share of participants classified as responders. The TES group had 28 responders among 38 participants, and the TES-SHAM group had 29 among 40. These counts are the basis for the posted comparison. The registry describes the outcome as a count of participants rather than a mean score.

What does a risk difference describe?

A risk difference expresses the contrast between two group response proportions on an absolute scale. The reported estimate is 0.012 for TES compared with sham TES. A value of zero would represent equal response proportions; positive and negative values indicate differences in opposite directions according to the comparison’s ordering. The interval from -0.185 to 0.209 spans zero, so the data do not precisely determine whether the response proportion is lower or higher with TES. The confidence interval is more informative than treating the point estimate alone as the result.

How do relative measures add context?

The registry also reports a relative risk of 1.016, with a confidence interval from 0.776 to 1.33, and an odds ratio of 1.062, with a confidence interval from 0.390 to 2.891. A relative risk compares response proportions as a ratio, while an odds ratio compares the odds of response. The no-difference reference for these ratio measures is 1. Both intervals include that reference. These summaries use different scales from the risk difference, but each reflects uncertainty in the comparison. They should not be interpreted as independent confirmations because they are calculated from the same outcome counts.

What does the p-value contribute?

The registry reports an unadjusted p-value of 0.906. A p-value describes how compatible the observed data are with a specified no-difference hypothesis under the statistical test’s assumptions. It is not the probability that the null hypothesis is true, and it does not give the probability that the result will replicate. The test name, exact test procedure, and any covariate adjustment are not reported in the registry record. The interval estimate is useful alongside the p-value because it conveys a range of effects compatible with the data rather than reducing the result to a threshold decision.

Why can binary outcomes lose information?

Classifying participants as responders or nonresponders makes the result straightforward to interpret as a count, but it compresses PHQ-9 information. Participants with different scores or degrees of change can fall into the same category, while participants close to either side of the response rule can be classified differently. The registry gives the scale range, the stated response criterion, and the percent-change metric, but does not report individual score distributions or continuous outcome analyses. Consequently, the posted binary result cannot describe the full pattern of score changes.

What is not specified about the analysis?

The registry does not report the trial’s prespecified statistical analysis plan, the specific test used for the primary comparison, adjustment for baseline measurements, or handling of missing outcome data. It reports one outcome measure and no secondary outcomes, and the analysis count is listed as zero even though a comparison is posted. The record does not explain that difference. The comparison should therefore be described using the reported estimates and counts, without attributing methods that are not documented.

General statistical context: with binary outcomes, the amount of information depends on both the number of participants and how often the outcome occurs. Confidence intervals can be broad when information is limited, leaving uncertainty about both the size and direction of a group difference. This is why the counts, point estimates, and intervals should be read together rather than relying only on a p-value or on whether the point estimate is positive.

General statistical context: randomization is intended to support a fair comparison by distributing participant characteristics across groups on average. The registry identifies the design as randomized, but does not describe the sequence generation, concealment, or implementation. It is therefore appropriate to note the randomized design without assuming details of its execution. Similarly, masking can reduce some sources of bias, but the practical effectiveness of masking and the identity of the masked groups are not reported in the registry record.

10. Confidence Intervals and Precision

The risk-difference estimate is 0.012, and its confidence interval runs from -0.185 to 0.209. A confidence interval describes uncertainty in an estimated effect under the statistical method used. It is not a range of individual participant outcomes, nor does it mean that every value inside the interval is equally likely. In this result, the interval covers zero and extends into both negative and positive differences. The posted data therefore do not pin down the direction of the group difference precisely.

The relative risk estimate is 1.016, with a confidence interval from 0.776 to 1.33. The odds ratio estimate is 1.062, with a confidence interval from 0.390 to 2.891. Their no-difference reference is 1, and both intervals include that value. The odds-ratio interval is especially broad on its reported scale, illustrating that the data allow a range of possible relative associations. These measures should be interpreted as estimates with uncertainty, not as exact properties of the intervention.

The posted outcome data include 38 participants in the TES group and 40 in the sham group, with 28 and 29 responders, respectively. The registry says these 78 participants met the minimum time and treatment criteria and provided the full complement of data. This outcome sample size and the breadth of the intervals are important context for interpreting the result. A point estimate near zero does not by itself show that the underlying difference is near zero; the interval also allows differences in either direction.

Confidence intervals describe statistical uncertainty under the analysis assumptions, but do not address every source of uncertainty. In particular, the registry does not report detailed procedures for missing data, the test used, or the prespecified analysis plan. The intervals also do not resolve questions about the ECT arm that was dropped or about outcomes beyond the recorded 1-2 weeks. Precision should therefore be judged for the posted TES-versus-sham response comparison, not for broader claims that the study did not directly compare.

11. 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 are illustrations based on the observed effect, not the trial’s original design calculations. The registry does not report the original sample-size justification or the assumptions used when the study was planned. For the illustration, the stated 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 set to the stated fraction of the observed effect.

The 80% power column gives the illustrated number of participants per arm for a design with 80% power under those assumptions and at the selected effect size. In plain terms, power is the probability of detecting an effect at least as large as the one specified if that effect is present and the assumptions hold. The 90% power column shows the corresponding planning count for 90% power. These are prospective planning quantities, not summaries of the trial’s achieved ability to detect an effect.

For 100% of the observed effect, the illustration gives 22,015 participants per arm for 80% power and 29,471 for 90% power. For 75% of the observed effect, it gives 39,274 participants per arm for 80% power and 52,576 for 90% power. For 50% of the observed effect, it gives 88,670 participants per arm for 80% power and 118,703 for 90% power. Smaller effects require more participants under these planning assumptions, which is why the illustrated counts rise as the target effect is reduced.

These figures are not observed power. They should not be used to explain the result as though the trial had a known probability of detecting its actual effect. They are planning illustrations derived from the observed effect and the stated assumptions; the trial’s own original design assumptions are not reported in the registry record.

12. 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 = 0.725; treatment proportion p₁ = 0.737; average p̄ = 0.731.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6272 = 1.2292.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6271 = 0.5278.
4. n = (1.2292 + 0.5278)² / (0.0118)² = 22,014.4, rounded up to 22,015 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 <- 0.725                          # control proportion
p1 <- 0.736842105263158                          # 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(3277846)
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 = 22,015 (80% power), 29,471 (90% power)
 75% of observed effect: n per arm = 39,274 (80% power), 52,576 (90% power)
 50% of observed effect: n per arm = 88,670 (80% power), 118,703 (90% power)
power.prop.test: 22014.4 
Simulated power at n = 22,015 per arm: 0.794 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one outcome measure and no secondary outcomes. It also lists no analysis records, although a primary comparison is posted. The record does not report a prespecified statistical analysis plan, a hierarchy of outcomes, or a strategy for adjusting inference when multiple outcomes or comparisons are considered. With one posted outcome, multiplicity cannot be assessed beyond noting that the registry does not document such a plan. The unadjusted p-value should be read as reported, without assuming any correction or other analysis procedure.

The registry states that 101 participants were enrolled, while the primary outcome population is 78 participants who met the minimum time and treatment requirements and provided the full complement of data. It does not report why the other enrolled participants are not represented in the outcome counts, whether their outcome information was unavailable, or how missing outcomes were handled analytically. No imputation method or sensitivity analysis for missing data is reported. This limits assessment of how the posted response comparison may depend on the participants included in the outcome summary.

The posted primary outcome denominators are 38 for TES and 40 for sham TES. The registry’s description of the 78 participants refers to a minimum time and minimum number of treatments, as well as a full complement of data. It does not report whether the primary analysis followed an intention-to-treat population, a per-protocol population, or another formally defined analysis population. These labels should not be inferred from the counts alone.

The safety summaries use denominators of 50 for TES and 51 for SHAM-TES, distinct from the primary outcome denominators. The registry does not explain the difference between these populations or provide details of their relationship to the outcome analysis group. The record also does not report handling of missing safety information or the method used to collect adverse events. These omissions make it difficult to reconstruct the analysis populations or assess the impact of missing information. The interpretation is therefore confined to the posted counts and estimates, with the population and missing-data uncertainties kept explicit.

14. 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 0% reporting threshold.

The registry reports serious adverse event counts of 0 among 50 participants at risk in the TES group and 0 among 51 participants at risk in the SHAM-TES group. It also reports 0 deaths in each group. The posted other-adverse-event counts are 0 among 50 at risk with TES and 0 among 51 at risk with SHAM-TES. No serious adverse event terms are listed.

These are registry counts for the recorded safety groups. They do not mean that the risk of an event is known to be zero: with no recorded events, the data do not establish that events cannot occur. The record does not report the event-collection procedures, duration of safety follow-up, or details about how events were classified. The safety denominators also differ from the primary outcome denominators of 38 and 40, and the reason is not reported in the registry record. The counts should therefore be read as the posted safety summary, not as a complete account of all possible harms or as a direct comparison of every enrolled participant.

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

The result describes a short-term, binary response comparison between TES and sham TES among the participants included in the posted outcome counts. The registry reports 28 responders among 38 participants assigned to TES and 29 among 40 assigned to sham. The estimated risk difference is 0.012, and its confidence interval extends from -0.185 to 0.209. The interval includes no difference as well as possible differences in either direction. The unadjusted p-value is 0.906. Together, these statistics show that the posted data do not distinguish the groups clearly on this response measure.

This finding is not proof that TES and sham TES have identical effects. The confidence interval is compatible with a range of effects, and the outcome sample comprises 78 participants rather than all 101 enrolled participants. The registry does not describe in detail why other enrollees are absent from the primary outcome counts or how missing outcome data were handled. The result also relies on a particular binary response definition based on the PHQ-9, so it does not summarize every possible change in symptoms or score.

The result does not answer whether TES can replace ECT. The registry’s post-study note says the ECT arm was dropped, leaving TES versus sham TES as the comparison. Nor does the result establish effects beyond the recorded timeframe of 1-2 weeks. No secondary outcomes are posted, and the registry does not give longer-term outcome data in this record.

General statistical context: a nonsignificant or imprecise comparison should not be translated into a claim of no effect. It indicates that the available comparison does not give a precise enough estimate to distinguish among the possibilities covered by its uncertainty interval. Conversely, a positive point estimate alone is not proof of a benefit. Interpretation depends on the study design, the endpoint definition, the population represented, and the uncertainty around the estimate.

The safest reading is narrow: the registry reports similar response counts in the two posted groups, with an estimated difference whose confidence interval includes zero and substantial uncertainty in both directions. The statistics describe this study’s posted result; they do not by themselves establish a broader clinical conclusion.

16. Why This Trial Matters Statistically

This trial is statistically informative because its initial question and its completed comparison are not the same. The original description included an ECT arm and an aim to consider Nexalin as an alternative to ECT. The registry’s post-study note says that arm was dropped, and the reported analysis is TES versus sham TES. Recognizing that change prevents the primary comparison from being interpreted as a direct test against ECT.

The endpoint also illustrates the distinction between a clinically framed response category and the underlying scale. A responder count is easy to understand, but it reduces PHQ-9 change to a binary classification. The posted result gives counts and comparisons for that classification, not a full account of score distributions or continuous change. The endpoint definition and its 1-2 week timeframe are therefore central to understanding what the result represents.

The risk difference and relative measures are accompanied by broad intervals that include their no-difference reference values. That makes uncertainty a key part of the result rather than a technical footnote. The point estimate alone could be mistaken for a settled direction; the intervals make clear that the data remain compatible with multiple possibilities. The sample-size illustration further shows how planning counts depend on the effect size selected, but those calculations are not the study’s original design assumptions and are not observed power.

Finally, the registry distinguishes enrollment, primary outcome, and safety denominators. The primary outcome is reported for 78 participants, while safety counts use groups of 50 and 51. The record does not explain these population differences. Keeping denominators visible is essential to assessing what each statistic summarizes and to avoiding claims that extend beyond the analyzed participants.

17. 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 outcome covers 78 participants, although 101 were enrolled. The registry says the 78 met minimum time and treatment requirements and provided the full complement of data, but it does not report why the other enrollees are absent from the outcome groups or how their outcomes were handled. This leaves uncertainty about the relationship between enrollment and the primary analysis population.

The study’s planned ECT arm was dropped, according to the registry’s post-study note. The posted comparison therefore cannot directly address TES versus ECT, despite the original description’s interest in TES as a possible alternative. The result is limited to TES compared with sham TES.

The primary endpoint is a binary response definition based on the PHQ-9, reported over 1-2 weeks. The record does not provide individual scores, continuous changes, further detail about the timing represented by “ex-take,” or longer-term outcomes. The response classification cannot capture the full range of scores and changes in the participants.

The registry does not report the original sample-size justification, detailed statistical analysis plan, exact test used, missing-data methods, or a formal definition of the analysis population. The posted risk-difference confidence interval is broad and includes differences in both directions. The safety counts use different denominators from the primary outcome counts, and the reason for that difference is not reported. These limitations constrain interpretation of both the estimated response contrast and the safety summaries.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: The Safety and Efficacy of Nexalin Trans-cranial Electrical Stimulation Stimulation for the Treatment of Depression — NCT03277846.
• Registry record last updated 2019-10-28; status last verified 2019-10.
• Results first posted 2019-10-28.
• 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.

21. Record Summary

NCT03277846 is a completed randomized, parallel-group study sponsored by the University of Pennsylvania. The registry lists quadruple masking, while the official title describes the study as double-blind. It enrolled 101 participants with depression referred to or considered for ECT and compared Nexalin transcranial electrical stimulation with sham TES after the planned ECT arm was dropped.

The primary outcome was treatment response over 1-2 weeks, defined using the PHQ-9. The posted outcome counts are 28 of 38 participants in the TES group and 29 of 40 in the sham group. The reported risk difference is 0.012, with a confidence interval from -0.185 to 0.209 and an unadjusted p-value of 0.906. The registry reports no serious adverse events or deaths in either safety group. The original sample-size assumptions, detailed analysis plan, and reasons for differences among the enrollment, outcome, and safety populations are not reported in the registry record.