Transcranial Electrical Stimulation for mTBI: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Transcranial Electrical Stimulation for mTBI (NCT03244475), a randomized na study. The primary outcome is Change in Abnormal Magnetoencephalography (MEG) Slow-Waves (1-4 Hz) Activity.

2. Clinical Question

The registry identifies the study as randomized, double-masked, and parallel-group. Those design labels describe the overall trial record; details of exactly how masking was implemented, how allocation was generated, and whether every comparison group was randomized are not reported in the registry record. The outcome population is also not identical to the enrollment description: the primary outcome notes that the number of TES participants analyzed differs from the number enrolled, and that some sham participants could choose to complete TES sessions after their original sessions. Further details about those participants and the resulting analysis groups are not reported in the registry record.

3. Trial Design

The trial record identifies NCT03244475, titled “Transcranial Electrical Stimulation for mTBI.” Its official title refers to passive electrical neurofeedback treatment and MEG and behavioral outcomes. The study is marked completed, with enrollment of 66. The registry lists a randomized, double-masked, parallel design; the phase is listed as not applicable. The sponsor is the VA Office of Research and Development.

The clinical description includes Veterans with mTBI and identifies PTSD as another condition of interest. The treatment arm is described as six weeks of TES, either IASIS neurofeedback treatment or Nexalin, with two to three sessions per week. The sham arm is described as sham treatment over six weeks, also with two to three sessions per week. A separate control group comprises matched Veterans who do not undergo treatment. The registry does not report separate results for IASIS and Nexalin, so the posted TES outcome cannot be used to distinguish their individual effects.

The primary outcome is a continuous measure of abnormal MEG slow-wave activity, expressed as a pre-treatment minus post-treatment difference. The endpoint description specifies a treatment period averaging six weeks. Behavioral measures are also listed, including pain, PTSD, post-concussion symptoms, memory, processing speed, executive function, attention, and impulsivity. The record gives some secondary outcome results, but not a full account of how all outcomes were analyzed.

Although the registry lists enrollment, the number analyzed varies across outcomes and arms. The primary endpoint description explicitly notes that the number of TES participants analyzed differs from the number enrolled. It also notes that some sham participants could elect to complete TES sessions after their originally assigned sessions. The registry does not report a complete participant flow, the reasons for missing outcome data, the detailed allocation procedure, or the trial’s original sample-size justification. The original statistical analysis plan and analysis-population definitions are 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

Analysis population for the primary outcome, as defined in the registry: \# of TES participants analyzed differs from the # of TES participants enrolled. mTBI veterans who were blindly placed in the TES Sham group had the option of completing TES sessions at the end of their original sessions. Therefore, some TES Sham participants opted to complete TES sessions, with questionnaires and pre-post MEG imaging.

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.

Population: mTBI Veterans enrolled in a blinded study group. At the end of their study sessions, they were informed of their study group. If they were originally in a sham group, they had the option of receiving TES sessions. Questionnaires and MEG imaging continued if they chose to receive actual TES sessions. Therefore, the number of analysis TES population (n=38) is higher than the number of enrolled participants since some participants completed sham treatments and then opted for TES treatments.

6. Primary Endpoint

The registry lists the primary outcome as Change in Abnormal Magnetoencephalography (MEG) Slow-Waves (1-4 Hz) Activity, measured over Baseline through end of treatment, an average of 6 weeks.

The primary endpoint measures change in abnormal magnetoencephalography (MEG) slow-wave activity in the delta band, defined in the record as 1-4 Hz. The study describes voxel-wise whole-brain MEG source imaging and reports activity on a natural-log scale in log(pA-m), where pA-m refers to pico Ampere-meter. The described scale ranges from 0-10, and greater source activity is said to indicate more serious injury.

The endpoint is calculated as the activity at the pre-TES examination minus the activity at the post-TES examination. Under this definition, a larger positive difference means a greater reduction in the abnormal slow-wave signal. The result is therefore oriented so that positive change is described as a favorable reduction in the signal, not as an increase in activity. The reported group values are means with standard deviations.

MEG is used because the study rationale concerns possible neural abnormalities that may not be apparent on conventional imaging. The registry describes resting-state MEG slow-wave source imaging as a potential marker of neuronal abnormalities in mTBI and presents the study as an investigation of neural changes associated with treatment. This rationale does not establish that MEG change is itself a clinical benefit or that it captures every relevant symptom or functional outcome. It is a measured imaging endpoint, and its relationship to participants’ lived symptoms and functioning must be considered separately.

The registry specifies a baseline-through-end-of-treatment window averaging six weeks. It does not report a minimum clinically important difference for this endpoint, nor does it provide an interpretation threshold for deciding what magnitude of change would matter to patients.

7. Results Posted in the Registry

• Transcranial Electrical Stimulation (TES): mean 1.80 versus 0.20 on control; difference 1.60 (95% CI 0.83 to 2.37), standardized effect d = 1.27; z-test p = <0.001.
• Control: mean 0.00 versus 0.20 on control; difference -0.20 (95% CI -0.87 to 0.47), standardized effect d = -0.21; z-test p = 0.556.

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.

The McGill Pain Questionnaire (MGPQ)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Transcranial Electrical Stimulation (TES): mean 14.80 versus -5.10 on control; difference 19.90 (95% CI 6.35 to 33.45), standardized effect d = 1.15; z-test p = 0.004.
  • Control: mean 0.00 versus -5.10 on control; difference 5.10 (95% CI -6.12 to 16.32), standardized effect d = 0.40; z-test p = 0.373.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Transcranial Electrical Stimulation (TES) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Control and the control. The interval gives the range of effects that remain compatible with the data.

Clinician-Administered PTSD Scale (CAPS-5)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Transcranial Electrical Stimulation (TES): mean 6.50 versus 4.20 on control; difference 2.30 (95% CI -5.67 to 10.27), standardized effect d = 0.19; z-test p = 0.572.
  • Control: mean 0.00 versus 4.20 on control; difference -4.20 (95% CI -9.87 to 1.47), standardized effect d = -0.69; z-test p = 0.147.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Transcranial Electrical Stimulation (TES) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Control and the control. The interval gives the range of effects that remain compatible with the data.

Post-Concussion Check List (PCL-5)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Transcranial Electrical Stimulation (TES): mean 14.90 versus 12.10 on control; difference 2.80 (95% CI -10.93 to 16.53), standardized effect d = 0.14; z-test p = 0.689.
  • Control: mean 0.00 versus 12.10 on control; difference -12.10 (95% CI -24.40 to 0.20), standardized effect d = -0.75; z-test p = 0.054.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Transcranial Electrical Stimulation (TES) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Control and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several domains, including pain, PTSD symptoms, post-concussion symptoms, verbal learning, processing speed, executive function, attention, and impulsivity. The registry reports nine posted secondary measures, while the detailed result summaries available for interpretation cover only part of that set. It does not report a complete account of results for every listed measure in the information analyzed.

Across the detailed summaries, the pattern is not uniform. The unadjusted recalculations do not show the same level of statistical evidence across all secondary comparisons, and the sponsor’s posted analyses use a nominal p-value for the available comparisons. This varied pattern does not provide a consistent secondary-outcome confirmation of the primary MEG finding. It also does not establish that the primary result lacks relevance: the primary endpoint and behavioral measures assess different constructs, and they should not be expected to move identically.

Secondary outcomes are usually interpreted as supportive or exploratory unless a clear testing hierarchy and multiplicity plan are reported. When many outcomes are tested, the chance of at least one nominally notable result can increase. A nominal p-value does not account for that broader testing context unless an adjustment or prespecified strategy is used. The registry does not report whether multiplicity was addressed, how the secondary measures were prioritized, or which analyses were prespecified.

Consequently, the secondary results should be read as additional descriptive evidence rather than as independent confirmation of treatment effect. Their interpretation is further limited by varying numbers analyzed across outcomes and by the absence of a full missing-data account. The registry does not report thresholds for clinically meaningful change for these measures, so statistical contrasts alone cannot establish the importance of any observed differences.

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

• The McGill Pain Questionnaire (MGPQ)
• Clinician-Administered PTSD Scale (CAPS-5)
• Post-Concussion Check List (PCL-5)
• California Verbal Learning Test-2nd Edition - Free Recall Total Correct T-score
• Wechsler Adult Intelligence Scale-4th Edition (WAIS-IV) Processing Speed Index
• Delis-Kaplan Executive Function System (DKEFS) - Trail Number/Letter Switching Scaled
• Connors Continuous Performance Task II (CPT-II) - Inattention Omissions T-Score
• Barratt Impulsivity Scale

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a mean change score on the MEG activity scale. For the simple recalculation, the group mean in the comparator arm is contrasted with the group mean in the TES arm, using the posted outcome summaries. A mean difference expresses the separation between group averages in the scale’s units. Because the endpoint is defined as baseline minus post-treatment activity, a positive difference for TES relative to sham points toward a larger reduction in abnormal signal for TES.

The recalculated comparison is unadjusted. It uses the posted group summaries and does not account for covariates, clustering, repeated measurements, or other modeling choices unless those are reflected in the summaries themselves. The registry does not report enough information to determine whether the sponsor’s analysis included adjustments beyond its stated Wilcoxon (Mann-Whitney) method. Therefore, the recalculation is useful as a transparent descriptive comparison, but it should not replace the sponsor’s own analysis.

A standard deviation describes how spread out individual observations are around a group mean. It is not the same as the standard error, which describes the uncertainty in an estimated mean. In general, greater variability makes a group mean less precise, while more observations can improve precision if other factors are similar. The posted outcome summaries include standard deviations for the treatment and sham groups. The untreated control has a reported mean of 0.0 and standard deviation of 0.0 in the primary result; this is a reference value in the posted summaries and should not be treated as evidence that the control group had no underlying variability in the broader population.

A confidence interval gives a range of values compatible with the data and the analysis assumptions. It conveys uncertainty around an estimate rather than the probability that a fixed effect lies within the particular interval. For the primary recalculation, the interval excludes zero, consistent with the unadjusted p-value. The sponsor’s interval is based on its own analysis and is not identical to the recalculated interval. Because the registry reports a discrepancy, the sponsor’s analysis takes precedence when describing the trial’s own inferential result.

The sponsor used a Wilcoxon (Mann-Whitney) procedure for the primary TES-versus-sham comparison. In general, this is a rank-based method for comparing distributions between independent groups. It does not require the analysis to be framed as a comparison of normally distributed means in the same way as a conventional two-sample mean test. The registry labels the reported parameter as a mean difference, but it does not provide further methodological detail about how that estimate and its confidence interval were obtained alongside the rank-based test. That missing detail limits direct comparison with the simple mean-based recalculation.

The recalculated p-value is unadjusted. A p-value measures how surprising the observed data, or data more extreme, would be under a specified null model and analysis procedure. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. Statistical significance also does not resolve design limitations, missing data, or uncertainty about the endpoint’s clinical meaning.

For the secondary outcomes, the registry lists continuous measures and reports Wilcoxon (Mann-Whitney) comparisons in some cases. The posted secondary results do not provide a complete statistical analysis plan, and the registry record does not report whether multiplicity adjustments were applied. When many outcomes are examined, some apparently notable results can occur by chance. A prespecified hierarchy or adjustment can help control that risk, but whether either was used is not reported in the registry record.

For these reasons, the most defensible reading separates three things: the sponsor’s trial analysis, the unadjusted recalculation from the posted summaries, and general statistical context. The recalculation helps readers understand the scale and direction of the group contrast; it is not a reconstruction of the trial’s full analysis. The record does not report the original statistical analysis plan, sample-size justification, interim analyses, covariate adjustment strategy, or detailed missing-data methods.

11. Confidence Intervals and Precision

The primary recalculated mean difference is 1.6, with a confidence interval that excludes zero. This indicates that, under the simple unadjusted calculation, the data are compatible with a positive difference in mean change between TES and sham. The interval is not a guarantee that the true difference falls within its bounds; it represents uncertainty under the assumptions of the calculation.

The sponsor reports a 95% confidence interval from 1.1 to 2.2 for its mean-difference estimate of 1.6. This interval is narrower than the recalculated interval, and the sponsor’s p-value is 0.01 rather than the recalculated p-value of <0.001. The difference arises in the context of different analysis procedures. The registry does not explain the discrepancy, so the sponsor’s result should be treated as the trial’s reported inference, while the recalculation remains a separate unadjusted check.

Precision depends on the amount of information, variation in the outcome, and the analysis used. The outcome standard deviations indicate variability in the observed groups, and the analyzed sample sizes differ across the listed arms and outcomes. The registry notes specifically that the number of TES participants analyzed for the primary endpoint differs from the number enrolled. Without a complete account of missingness and participant flow, it is difficult to judge how that affects uncertainty or the representativeness of the analyzed groups.

The interval and p-value describe statistical uncertainty, not clinical relevance. The registry does not report a threshold for a meaningful change in MEG activity, so the interval cannot be judged against a stated clinical benchmark. Nor does the imaging estimate establish the precision of effects on symptoms or functioning. Those outcomes require their own estimates and interpretation.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For these continuous-outcome comparisons, the figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning scenarios consider detecting 100%, 75%, or 50% of the observed effect.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect is real and the assumptions hold. The 90% power column represents a higher target chance of detection and therefore generally requires more participants per arm. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants. The figures are not observed power and do not describe the probability that the completed trial’s result is correct.

These illustrations are especially sensitive to the observed effect used as their starting point. An effect estimate from a study can be unstable, particularly when the analyzed groups are limited or when outcome populations differ. The registry does not report the original sample-size justification or the assumptions used when planning this trial. The illustrated figures should therefore be read as conditional planning examples, not as evidence that the trial was designed with those targets or that a future study must use those exact sizes.

The corresponding curve is a visual aid to the same planning relationship: higher power targets and smaller effects require greater sample sizes under the stated assumptions. It should not be read as a plot of achieved power or as a forecast that automatically accounts for missing data, allocation constraints, analysis choices, or differences between future participants and those in this study.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 1.600; pooled standard deviation σ = 1.264.
2. n = 2 × (1.96 + 0.842)² × 1.264² / 1.600² = 9.8, rounded up to 10 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
delta <- 1.6                      # observed difference in means
sigma <- 1.26371718832794                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3244475)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 10 (80% power), 14 (90% power)
 75% of observed effect: n per arm = 18 (80% power), 24 (90% power)
 50% of observed effect: n per arm = 40 (80% power), 53 (90% power)
power.t.test: 10.8 
Simulated power at n = 10 per arm: 0.765 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 sponsor’s reported primary comparison uses a Wilcoxon (Mann-Whitney) superiority analysis for TES versus TES sham. It reports a mean difference of 1.6, a 95% confidence interval from 1.1 to 2.2, and p = 0.01. The registry’s own analysis is the primary trial result for interpretation.

The unadjusted recalculation uses the posted group means and standard deviations. It also estimates a mean difference of 1.6, but gives a different confidence interval and p-value: the recalculated interval is wider, and its unadjusted p-value is <0.001. This is a genuine discrepancy between the sponsor’s reported inference and the simple recalculation; the registry does not explain its source. The analysis procedures are not identical, and the record does not provide sufficient detail to reconstruct the sponsor’s calculation.

The sponsor’s own analysis takes precedence. The recalculation is best used as a transparent check on the direction and scale of the contrast, not as a replacement, correction, or competing primary result. The agreement in the point estimate does not eliminate the difference in uncertainty estimates or testing results. Neither analysis determines whether the MEG change is clinically meaningful, and both pertain specifically to the TES-versus-sham comparison on the primary imaging endpoint.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes in addition to the primary MEG endpoint. Testing several outcomes creates a multiplicity concern: even when there is no true effect across the measures, some results may appear notable by chance. Statistical approaches can address this through a prespecified hierarchy, adjusted significance thresholds, or other planned procedures. Whether any such approach was used is not reported in the registry record.

The available results include unadjusted recalculations and sponsor-reported secondary analyses, but the record does not provide a complete statistical analysis plan. The prespecified status of each endpoint, the order in which outcomes were tested, any subgroup analyses, and any adjustments for multiple comparisons are not reported in the registry record. Without those details, secondary p-values should be treated as nominal and interpreted cautiously rather than as a definitive set of independent findings.

Missing-data reporting also limits interpretation. The primary outcome description states that the number of TES participants analyzed differs from the number enrolled. It further explains that some participants assigned to TES sham had the option of completing TES sessions after their original sessions. The registry does not provide a complete participant flow or explain how those participants were handled in each analysis. Reasons for missing outcomes, the extent of missingness by group, and the methods used to address missing data are not reported in the registry record.

Analysis-population definitions are also not reported in sufficient detail. The record does not specify whether the primary analysis followed intention-to-treat principles, used a per-protocol population, or applied another rule for assigning participants to analysis groups. That matters because post-assignment treatment choices and missing outcome data can affect how group comparisons are interpreted. The registry also does not report interim analyses or stopping rules. These omissions do not prove that such procedures were absent; they mean their use cannot be established from the registry record.

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 0% reporting threshold.

The registry reports zero serious adverse events in the TES, TES sham, and control groups. It also reports zero other adverse events and zero deaths in each group. The corresponding at-risk counts are reported separately for each group in the safety data.

These figures describe events recorded in the registry; they do not show that risk was absent. A zero count can occur even when an event is possible, and the ability to identify uncommon harms depends on the amount and duration of observation. The registry record does not provide detailed event definitions, collection procedures, observation time by participant, or a narrative describing safety monitoring. It also does not provide information that would establish whether all events were captured equally across groups.

The safety results should therefore be read narrowly: no serious or other adverse events, and no deaths, are recorded in the posted group summaries. They do not establish that TES is free of risk, and they do not support conclusions about safety beyond the groups and observation recorded.

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

The primary result describes a difference in change in abnormal MEG slow-wave activity between TES and sham. The endpoint is defined so that a larger positive change corresponds to a larger reduction in the abnormal signal. The posted group means and the sponsor’s superiority analysis both point toward a larger reduction in the TES group than in the sham group during the treatment period averaging six weeks.

That statistical finding is specific to this imaging measure and comparison. It does not establish that every participant experienced a reduction, that symptoms improved, or that daily functioning changed. It does not show that the MEG measure is a validated substitute for patient-important outcomes, nor does the registry provide a threshold for a clinically meaningful change. The behavioral outcomes address related but distinct domains and do not provide a uniform pattern of confirmation.

The result also does not distinguish IASIS neurofeedback from Nexalin. The TES arm description includes both approaches, but separate outcome estimates are not reported. The findings cannot be attributed to either device or treatment approach individually on the basis of the registry record.

The matched untreated control is not the same comparator as sham. A comparison with sham addresses the treatment contrast in a way that an untreated reference does not. The control results should not be substituted for the randomized treatment comparison, and the record does not provide enough detail to establish the allocation process for every group.

Finally, the result does not establish longer-term effects or generalize automatically to all people with mTBI, to people with PTSD, or to clinical settings beyond the study population. Follow-up beyond the reported treatment timeframe, generalizability details, and clinically meaningful thresholds are not reported in the registry record. The appropriate conclusion is about the recorded MEG outcome, the posted comparison, and its uncertainty—not a broad claim about treatment effectiveness.

18. Why This Trial Matters Statistically

This trial is statistically interesting because it places an imaging endpoint at the center of a treatment comparison for mTBI. The primary measure is not a symptom score but a quantitative change in MEG slow-wave activity, with a clear directional definition: greater positive change means a greater reduction in the abnormal signal. That makes it possible to distinguish the measured imaging question from broader claims about recovery.

The record also illustrates why analysis method matters. The sponsor reports a rank-based superiority analysis, while the simple recalculation from summary statistics uses a mean-based contrast. The point estimates agree, but the uncertainty and p-values differ. Recognizing that distinction prevents a recalculation from being mistaken for the sponsor’s trial analysis and highlights the value of a complete statistical analysis plan.

Another important issue is the separation of primary and secondary evidence. A primary endpoint can answer a focused question, while numerous behavioral outcomes may be informative but raise multiplicity concerns. Without a reported hierarchy or adjustment strategy, secondary findings are better treated as exploratory or supportive. The reported differences in analyzed populations and the option for some sham participants to complete TES further emphasize the importance of participant flow and analysis-population definitions.

More broadly, the record shows how precision, clinical meaning, missingness, and safety reporting all shape interpretation. Statistical evidence of a difference on an imaging scale is not equivalent to evidence of meaningful symptom change. A complete account of follow-up, outcome thresholds, missing-data handling, and analysis decisions would help readers judge how far the result can be taken.

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.

Several trial-specific limitations affect interpretation. The primary endpoint description notes that the number of TES participants analyzed differs from the number enrolled. It also states that some people assigned to sham could choose to complete TES sessions after their original sessions. The registry does not report how those choices affected analysis-group classification, how many participants made that choice, or how the resulting data were handled.

Outcome populations vary across the posted results. The registry does not provide a full participant flow, reasons for missing outcome data, or a detailed account of missing-data methods. As a result, it is not possible to assess from the record whether missingness differed between groups or whether the analyzed participants represent all enrolled participants.

The TES arm description includes IASIS and Nexalin, but separate results for those approaches are not reported. The outcome estimate therefore cannot identify which approach contributed to the observed comparison. The registry also does not report a clinically meaningful threshold for the MEG change measure, limiting interpretation of the size of the difference beyond its statistical direction and uncertainty.

The primary sponsor analysis and the unadjusted recalculation differ in their confidence intervals and p-values. The sponsor’s result takes precedence, but the record does not provide enough detail to reconcile the discrepancy. The analysis plan, covariate strategy, multiplicity procedures, and original sample-size justification are not reported in the registry record. In addition, the record does not establish longer-term outcomes or provide a basis for broad generalization beyond the described Veterans and study setting.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Transcranial Electrical Stimulation for mTBI — NCT03244475.
• Registry record last updated 2024-01-18; status last verified 2023-12.
• Results first posted 2024-01-18.
• 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

NCT03244475 is a completed, randomized, double-masked, parallel study of TES for mTBI, with enrollment of 66. The registry describes TES, sham treatment, and an untreated matched control. Its primary endpoint is the pre-treatment minus post-treatment change in abnormal MEG slow-wave activity over a period averaging six weeks.

The sponsor reports a TES-versus-sham superiority result for the primary endpoint, with a mean difference of 1.6, a 95% confidence interval from 1.1 to 2.2, and p = 0.01. The unadjusted recalculation gives a different interval and p-value; the sponsor’s own analysis takes precedence. Secondary outcomes show a less consistent pattern, and multiplicity handling is not reported.

The registry notes that analyzed numbers differ from enrollment and that some sham participants could elect to complete TES sessions. Detailed missing-data methods, analysis-population definitions, and the original sample-size justification are not reported in the registry record. The findings should be interpreted as specific to the posted MEG comparison rather than as proof of clinical benefit or long-term effect.