Enhancing Cognitive Control in Mild Cognitive Impairment Via Non-invasive Brain Stimulation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Enhancing Cognitive Control in Mild Cognitive Impairment Via Non-invasive Brain Stimulation (NCT04647032), a randomized na study. The primary outcome is Divided Attention Performance.

2. Clinical Question

3. Trial Design

The registry describes a randomized, quadruple-masked, parallel-group trial. The two listed arms were the Theta Stimulation Group and the Delta Stimulation Group. The theta group received 6 Hz stimulation, while the delta group received 1 Hz stimulation. The posted primary comparison is between these two active stimulation conditions; the record does not describe a sham or untreated comparison arm.

The registry lists an enrollment of 30 and marks the study as completed. The posted primary outcome analysis includes 14 participants in the theta group and 13 in the delta group. The primary outcome population is described as participants who completed the full protocol. The record does not explain the relationship between the enrollment figure and the numbers analyzed, or give reasons that participants may not have contributed to the primary outcome analysis.

The primary outcome was measured at post-tACS follow-up, described as 1-day follow-up and approximately 1 week after baseline. The registry lists the study start as 2021-01-11 and primary completion as 2021-12-31. The study phase is recorded as NA. The sponsor is the University of California, San Francisco.

Randomization can help make groups comparable on average, but it does not ensure that every feature is balanced in a small trial. Masking is intended to limit influences on participants, study staff, or assessments, but the record does not describe who was masked or how masking was implemented. Details of the randomization procedure, allocation concealment, stimulation delivery, and protocol deviations are not reported in the registry record. The 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

Analysis population for the primary outcome, as defined in the registry: Only data from participants who completed the full protocol were analyzed.

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 Divided Attention Performance, measured over Post-tACS (1-day follow-up), approximately 1 week after baseline.

The primary endpoint is divided-attention performance, measured as the difficulty level achieved during perceptual discrimination while participants engaged with the Akili AKL-T01 task. The registry states that higher performance is better. The outcome is reported as a mean with a standard deviation for each group, which treats the measure as continuous for the posted summary.

This outcome is relevant to the stated project goal because divided attention involves coordinating attention while performing a task, and the project aims to study cognitive control in adults with mild cognitive impairment. That connection describes why the measure may be of interest; it does not establish that the task captures every aspect of cognitive control or everyday functioning. The record does not report validation details, a clinically meaningful difference, or a threshold for interpreting a change as important to participants.

The assessment time is described as post-tACS, at a 1-day follow-up approximately 1 week after baseline. This timing focuses the result on performance at that follow-up rather than on long-term change. The registry’s primary analysis population is limited to participants who completed the full protocol. That restriction is important when interpreting the endpoint because the posted mean describes the analyzed completers, not necessarily every participant enrolled in the study.

7. Results Posted in the Registry

• Delta Stimulation Group: mean 9.31 versus 9.29 on control; difference 0.02 (95% CI -1.95 to 1.99), standardized effect d = 0.01; z-test p = 0.984.

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.

Instrumental Activities of Daily Living (IADL)

• 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:
  • Delta Stimulation Group: mean 4.00 versus 3.92 on control; difference 0.08 (95% CI -0.07 to 0.23), standardized effect d = 0.38; z-test p = 0.302.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Delta Stimulation Group and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary result concerns instrumental activities of daily living, or IADL, measured as a score on a scale at the same post-tACS follow-up described for the primary outcome. Its group summaries and comparison should be considered alongside, but not substituted for, the divided-attention result. The outcomes address different aspects of performance, so a pattern on one measure does not automatically confirm or contradict a pattern on the other.

The registry lists IADL among the secondary outcomes and posts an IADL comparison, but it does not report a set of secondary analyses with a stated model or analysis plan. The secondary result does not provide independent confirmation of the primary result simply because it concerns another outcome. Agreement or disagreement across outcomes can be informative, but interpretation depends on prespecification, measurement properties, and how many outcomes or comparisons were examined.

Unadjusted secondary results carry less weight because they may be among multiple opportunities to observe an apparently notable pattern. In general, when many outcomes are tested, the chance of obtaining at least one unusual result can increase unless the analysis accounts for multiplicity or a hierarchy of hypotheses is prespecified. The registry record does not report a multiplicity adjustment or a hierarchy for these outcomes. Therefore, secondary findings are best treated as descriptive or exploratory rather than as stand-alone evidence establishing an effect.

The primary and secondary outcomes also have different meanings. Divided-attention performance is a task-based measure of difficulty achieved during perceptual discrimination. IADL is reported as a score on a scale, but the registry does not give details about the scale’s range, interpretation, or clinically meaningful change. Without those details, the statistical contrast cannot by itself establish the practical importance of a difference. The broader pattern should therefore be understood cautiously: the secondary measure adds context, but does not resolve the uncertainty in the primary comparison or establish a general effect on everyday functioning.

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

• Instrumental Activities of Daily Living (IADL)
• Instrumental Activities of Daily Living (IADL)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is summarized as a mean and standard deviation in each randomized group. A mean describes the group’s average performance on the continuous task measure. A standard deviation describes how dispersed individual scores are around that group average; it is not the uncertainty in the estimated mean. The registry lists a standard deviation of 2.83 for the theta group and 2.4 for the delta group. Those figures describe observed variability in the analyzed groups, while the confidence interval for the group contrast describes uncertainty in the estimated difference.

The reported contrast is a mean difference, with delta stimulation compared against theta stimulation. Its estimate is 0.02. The direction of the contrast matters: a positive value means the delta-group mean is higher, and a negative value means the theta-group mean is higher. Since the endpoint is described as better at higher difficulty levels, the sign can be understood in that context. The estimated difference is small, but its precision must be judged alongside the confidence interval, not from the point estimate alone.

What does the confidence interval express?

In general, a confidence interval is a range of values produced by a statistical procedure that reflects uncertainty about an estimated quantity. It is not a range containing every individual participant’s score, and it does not mean that each value within the interval is equally plausible. For this comparison, the reported interval extends from -1.955 to 1.995. It includes no difference and values favoring either group. Its breadth indicates that the estimate does not tightly determine the size or direction of the underlying group contrast.

How should the p-value be read?

The unadjusted p-value is 0.984. In general, a p-value is calculated under a statistical model that specifies a reference hypothesis, commonly a hypothesis of no group difference. It indicates how unusual data at least as incompatible with that reference would be under the model. It is not the chance that the reference hypothesis is true, nor does it measure the probability that a result will replicate. The registry does not report the exact test, model, or analysis code used, so the posted p-value should be treated as the registry’s reported unadjusted result rather than as a fully described analysis.

Why does the analysis population matter?

The primary outcome description says that only participants who completed the full protocol were analyzed. In general, analyzing only completers can produce a result that differs from an analysis retaining everyone assigned to a group, especially if completion is related to outcome or group assignment. The record does not report reasons for non-completion, missing outcome values, or an intention-to-treat analysis. It is therefore not possible to determine from the registry how missing observations were handled or whether the completer analysis could be affected by selection.

What can randomization and masking contribute?

In general, random assignment aims to reduce systematic differences between groups at the start of a trial, while masking can reduce the influence of expectations or knowledge of assignment. The registry identifies the study as randomized and quadruple-masked, but does not give the procedures or identify which roles were masked. These design labels do not replace information about baseline characteristics, adherence, withdrawals, or implementation. Nor do they guarantee that chance imbalances cannot occur.

What analysis details remain unknown?

The registry record does not report whether the primary comparison was adjusted for baseline performance, the precise statistical model, assumptions checked, or a prespecified testing hierarchy. It also does not report an interim analysis plan. These details matter because choices about adjustment, variance assumptions, and how multiple outcomes are handled can affect estimates and their interpretation. No alternative model or recalculated result is presented as a substitute for the sponsor’s analysis. The posted numbers support a descriptive reading of the comparison, while the absence of methodological detail limits independent evaluation of how the inferential results were obtained.

In general, a small estimated difference and a large p-value should not be treated as proof of equivalence. Evidence of equivalence requires a prespecified margin and an analysis designed to assess whether the confidence interval falls within that margin. No such margin or equivalence analysis is reported in the registry record. Likewise, a nonsignificant result does not establish that a meaningful difference is absent; the confidence interval and the study’s precision remain central to interpretation.

11. Confidence Intervals and Precision

The primary mean difference is 0.02, and its 95% confidence interval runs from -1.955 to 1.995. The interval is centered near the reported estimate and includes values below and above no difference. This means that the posted data do not precisely identify a single direction or magnitude for the difference between the groups. The point estimate alone can look definitive if read without its interval; the interval makes clear that substantial uncertainty remains.

In general, a confidence interval conveys uncertainty in an estimate under the analysis assumptions. It does not describe the spread of individual scores, which is summarized by the group standard deviations. It also does not assign a probability to a particular treatment effect after the data have been observed. The registry does not report the detailed model or assumptions used to calculate the interval, so its interpretation depends on the analysis as implemented by the study team.

The reported group sizes for the primary analysis are 14 in the theta group and 13 in the delta group. The primary outcome population is defined as participants who completed the full protocol. The limited analyzed group sizes and completer restriction are relevant when considering precision and generalizability, but the record does not describe missing observations or participant characteristics well enough to evaluate potential selection effects.

The interval should not be read as evidence that the groups are equivalent: no equivalence margin is reported. Nor does it show that either group had no change from baseline, since the primary contrast is between groups at follow-up and no baseline result is posted for this outcome. The appropriate reading is that the observed mean difference is close to zero, while the uncertainty around it allows a range of possible differences in either direction.

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. The registry record describes the planning illustration as based on a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. These are planning assumptions for the illustration; the trial’s original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding per-arm number for a design with a 90% chance. These are prospective design quantities, not measurements of how likely the completed trial was to find a result. The posted sample-size illustration is not observed power.

The rows consider planning for 100%, 75%, and 50% of the observed primary effect. The figures rise as the assumed effect becomes smaller: a smaller difference is harder to distinguish from random variation and generally requires more participants to detect with the same planned power. The very small observed primary mean difference leads to very large planning figures when that difference, or a fraction of it, is used as the target. Those numbers should not be mistaken for a recommendation or for the number the original investigators intended to recruit. They are illustrations derived from the observed result under the stated assumptions.

For interpretation, the central point is that the planning table connects a chosen target effect to a per-arm sample size under specified assumptions. It does not show that the completed study had a particular probability of success, and it cannot establish that the original design was adequately or inadequately sized. The original protocol’s target effect and design rationale are not reported in the registry record.

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 = 0.020; pooled standard deviation σ = 2.632.
2. n = 2 × (1.96 + 0.842)² × 2.632² / 0.020² = 271,941.2, rounded up to 271,942 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 <- 0.0200000000000014                      # observed difference in means
sigma <- 2.63238067155949                     # 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(4647032)
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 = 271,942 (80% power), 364,053 (90% power)
 75% of observed effect: n per arm = 483,452 (80% power), 647,204 (90% power)
 50% of observed effect: n per arm = 1,087,765 (80% power), 1,456,209 (90% power)
power.t.test: 271942.2 
Simulated power at n = 271,942 per arm: 0.801 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome and secondary outcomes that include instrumental activities of daily living. It also reports multiple outcome measures and no secondary analyses in the analysis listing. The posted IADL summary comparison is therefore not accompanied by a registry-listed analysis description that would clarify how that result was planned or tested. The record does not report a prespecified hierarchy among outcomes, a family of primary hypotheses, or a multiplicity adjustment.

In general, testing several outcomes or contrasts creates more opportunities for chance findings. A multiplicity strategy can control how strongly evidence is interpreted across a set of tests, but the appropriate approach depends on which questions were prespecified and how outcomes are related. Without a reported strategy, unadjusted secondary p-values should be interpreted cautiously. The primary comparison is the central posted result, but the record does not provide enough analysis-plan detail to evaluate whether other planned comparisons could affect its interpretation.

The primary endpoint population is described as participants who completed the full protocol. The record does not explain whether outcome data were missing for other participants, why any participants did not complete the protocol, or how missing data were handled. It does not report an analysis including all randomized participants or sensitivity analyses examining alternative assumptions about missing outcomes. These omissions prevent assessment of whether completer selection could have influenced the observed group means or comparison.

The registry record also does not report the original sample-size justification, a detailed statistical analysis plan, or an interim analysis plan. It does not specify whether the primary comparison was adjusted for baseline values or other covariates, nor does it describe checks of model assumptions. Those details matter for understanding the intended estimand and the robustness of the reported uncertainty. Their absence does not prove that the study team lacked such plans; it means they are not reported in the registry record.

For a small randomized study, transparent reporting of allocation, analysis populations, missingness, and all prespecified outcomes is especially useful. Without those details, readers can describe the posted estimates and their uncertainty, but cannot fully reconstruct the intended analysis or assess the risk of selective reporting. The record supports a cautious, outcome-specific interpretation rather than a comprehensive evaluation of every planned analysis.

15. 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 adverse-event figures list 15 participants at risk in each group for serious adverse events and other adverse events. The registry reports zero serious adverse events and zero other adverse events in the theta group, and the same counts in the delta group. It also reports zero deaths in each group. The record lists no serious adverse-event terms.

These figures describe what was recorded for the listed groups in the registry. They do not establish that no adverse events of any kind occurred beyond the categories and reporting represented there, and they do not quantify the frequency of events that were not recorded or reported. The safety groups’ at-risk counts are not the same as the primary outcome analysis population, which is described as participants completing the full protocol.

Zero recorded events in a small trial cannot rule out uncommon harms or characterize safety across broader populations or longer follow-up. The registry record does not describe how adverse events were defined, how they were solicited, the duration of safety monitoring, or whether events were assessed for relatedness to stimulation. The counts should therefore be read as the registry’s reported safety summary, not as a complete account of all possible risks.

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

The primary result is an estimate of the difference in mean divided-attention performance between participants assigned to theta stimulation and those assigned to delta stimulation at the specified follow-up. The posted estimate is 0.02, with a confidence interval from -1.955 to 1.995. The two group means are close, but the interval indicates substantial uncertainty about the size and direction of the underlying difference.

This does not establish that the two stimulation conditions are equivalent. Equivalence requires a meaningful margin set in advance and an analysis designed to show that the plausible differences fall within that margin; neither is reported in the registry record. The result also does not establish that either stimulation condition improved performance, because the primary contrast is between groups at follow-up rather than a reported change from baseline or a comparison against no stimulation.

The study asks a focused question about one task-based outcome in adults with mild cognitive impairment. It does not, on its own, answer broader questions about cognitive control across settings, daily functioning, durability of any change, or effects in populations not represented in the analyzed participants. The secondary IADL result provides another measure, but its presence does not overcome limitations in precision or establish a broad functional effect.

The registry identifies a randomized and quadruple-masked design, features intended in general to support a fair comparison and reduce bias. However, the record does not report sufficient detail about implementation, missing outcomes, baseline characteristics, or analysis methods to fully assess those protections. The primary analysis includes only participants who completed the full protocol, which may limit how well the result represents everyone enrolled or assigned.

The most defensible interpretation is therefore bounded: the posted data show a small estimated difference between the two groups on the measured divided-attention task, but the confidence interval is broad and includes differences in either direction. The result is informative as a report of this comparison, yet it does not settle whether a practically important difference exists or what either condition means for broader cognitive or everyday outcomes.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the distinction between an estimated effect and the precision of that estimate. The primary mean difference is close to zero, but the confidence interval is wide enough to include a range of possible contrasts. A point estimate alone cannot establish that the true difference is negligible. Equally, a result that does not give strong evidence against a no-difference model is not proof that the groups are the same.

The comparison is between two stimulation frequencies, not between stimulation and no stimulation. That design defines the question the randomized contrast can address. Readers should not extend the result to a different comparator or to broader treatment claims. The task-based endpoint also makes the estimand specific: it concerns difficulty achieved during a perceptual discrimination task at a stated follow-up.

The record highlights how analysis-population definitions affect interpretation. The primary result uses participants who completed the full protocol, while the registry does not describe missing outcomes or reasons for non-completion. Reporting the analyzed population is useful, but more information is needed to understand whether the completer restriction could have introduced selection.

Finally, the sample-size illustration demonstrates how planning depends on the target effect. Smaller effects require more participants to detect under the stated planning framework. Such calculations can help readers understand the relationship between precision and design, but they do not reveal the original investigators’ rationale or quantify the completed study’s chance of success. The original design assumptions are not reported in the registry record. Taken together, these features make the trial a useful example of why effect estimates, uncertainty, analysis populations, and design assumptions need to be considered together.

18. 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 registry record leaves important context for this specific trial unreported. It does not describe the randomization method, allocation concealment, or how quadruple masking was implemented. It also does not provide baseline characteristics or baseline divided-attention results. Without those details, readers cannot assess the groups’ observed comparability at baseline or determine whether the primary comparison accounted for baseline performance.

The primary analysis is restricted to participants who completed the full protocol. The record does not explain the relationship between enrollment and the analyzed group sizes, give reasons for non-completion, or state how missing outcomes were handled. This limits assessment of whether the analyzed participants represent everyone assigned to the groups. No intention-to-treat result or sensitivity analysis is reported in the registry record.

The outcome description identifies the task and says higher performance is better, but the record does not report the measure’s range, test-retest properties, or a clinically meaningful difference. That makes it difficult to translate the numerical contrast into practical importance. The reported follow-up is shortly after stimulation; longer-term performance is not addressed by this primary result.

The record does not provide detailed stimulation procedures, adherence information, protocol deviations, or the statistical model used for the primary comparison. It also does not report a multiplicity strategy, an original sample-size justification, or an interim analysis plan. These omissions constrain independent appraisal of analysis choices and selective reporting. The safety summary likewise lacks detail on event definitions and monitoring procedures. These are limitations of what the registry record reports, not evidence that the study team did not collect or consider the information.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Enhancing Cognitive Control in Mild Cognitive Impairment Via Non-invasive Brain Stimulation — NCT04647032.
• Registry record last updated 2023-05-11; status last verified 2023-04.
• Results first posted 2023-05-11.
• 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.

22. Record Summary

The registry record describes a completed randomized, quadruple-masked, parallel-group study sponsored by the University of California, San Francisco. It compares 6 Hz theta stimulation with 1 Hz delta stimulation in adults with mild cognitive impairment. Enrollment is listed as 30, and the primary outcome analysis includes participants who completed the full protocol.

The primary outcome is divided-attention task performance at post-tACS follow-up, approximately 1 week after baseline. The posted mean difference is 0.02, with a 95% confidence interval from -1.955 to 1.995 and an unadjusted p-value of 0.984. The interval indicates substantial uncertainty about the size and direction of the group difference.

An IADL secondary result and safety counts are also reported. The record does not report the original sample-size justification, detailed statistical analysis methods, missing-data handling, or a multiplicity strategy. Interpretation is therefore best kept specific to the posted outcomes and the information documented in the registry.