Preventing Epilepsy Using Vigabatrin In Infants With Tuberous Sclerosis Complex: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Preventing Epilepsy Using Vigabatrin In Infants With Tuberous Sclerosis Complex (NCT02849457), a randomized phase 2 study. The primary outcome is Cognitive Assessment Scores and Developmental Impact.

2. Clinical Question

3. Trial Design

PREVeNT is described in the registry record as a phase IIb, prospective, multicenter, randomized, placebo-controlled, double-blind clinical trial. The masking entry is triple, and the allocation and model entries describe a randomized, parallel-group design. The study concerned infants with tuberous sclerosis complex and the prevention of seizures, with developmental outcomes also assessed.

The brief study summary describes a goal of enrolling 80 infants younger than 6 months before their first seizure. The registry lists enrollment of 84 and records the study as completed. It does not report the original design assumptions behind the enrollment goal or the sample-size justification.

All participants started in the Watchful Waiting group while being followed. Randomization occurred only when EEG epileptiform activity was detected. Participants assigned to Early Vigabatrin received vigabatrin; participants assigned to Delayed Vigabatrin received matching placebo until the treatment conditions described in the record were met. The record also describes a Watchful Waiting group for participants who did not develop EEG abnormalities or clinical seizures during the study. Some participants in that group are listed separately as receiving open-label vigabatrin.

The primary endpoint was the Bayley cognitive scale composite score at 24 months. Secondary outcomes included seizure occurrence, time to first clinical seizure, drug-resistant epilepsy, developmental and autism assessments, adverse events, and an EEG biomarker. Details of the methods for all outcomes, including any interim analyses or a full statistical analysis plan, 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.

Enrolled, Pre-randomized Period

Reasons for not completing this period:

Randomized Period

Analysis population for the primary outcome, as defined in the registry: The analysis population was the intent to treat population. Three participants withdrew prior to 24 months of age, and one participant did not complete the Bayley assessment at 24 months.

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 Cognitive Assessment Scores and Developmental Impact, measured over 24 months.

The primary endpoint was the standardized Cognitive scale score from the Bayley Scales of Infant and Toddler Development- Third Edition at 24 months. It is a continuous developmental measure: the posted results give a mean score and standard deviation for each group. The record describes a score range of 55 to 145, with a scale mean of 100 and standard deviation of 10. Higher scores indicate better performance on the cognitive assessment.

This endpoint was used to compare developmental outcomes after early versus delayed treatment. A standardized assessment gives a common scale for describing performance across participants, while the 24-month assessment supplies the specified time point for the primary outcome. The registry states that the score is derived from observed and elicited performance on cognitive tasks and calculated according to the measure's manual.

The primary analysis population is described as intent to treat. Three participants withdrew before 24 months of age, and one participant did not complete the Bayley assessment at 24 months. The record does not report further detail about how missing scores were handled in the sponsor's analysis. The posted means for the Watchful Waiting groups offer descriptive context, but the registry's reported primary comparison is between the randomized Early Vigabatrin and Delayed Vigabatrin groups.

7. Results Posted in the Registry

• Early Vigabatrin: mean 80.90 versus 83.90 on control; difference -3.00 (95% CI -12.07 to 6.07), standardized effect d = -0.18; z-test p = 0.517.
• Watchful Waiting (Control Group): mean 97.30 versus 83.90 on control; difference 13.40 (95% CI 1.16 to 25.64), standardized effect d = 0.78; z-test p = 0.032.

8. Secondary Efficacy Endpoints

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

Number of Subjects That Develop Seizures When Treated With Study Drug During the Randomized Phase of the Study.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Early Vigabatrin: 69.0% (20/29) versus 73.1% (19/26) on control; risk difference -4.1 percentage points (95% CI -28.1 to 19.9), risk ratio 0.94 (0.67–1.32); unadjusted two-proportion z-test p = 0.737.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Early Vigabatrin and the control. The interval gives the range of effects that remain compatible with the data.

Time to the Subject's First Clinical Seizure From Randomization

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • Delayed Vigabatrin (Placebo) vs Early Vigabatrin: hazard ratio 0.59 (95% CI 0.31–1.14), reported p = 0.117 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Delayed Vigabatrin (Placebo) vs Early Vigabatrin and the control. The interval gives the range of effects that remain compatible with the data.

Count of Participants With Drug Resistant Epilepsy at 24 Months of Age.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Early Vigabatrin: 48.3% (14/29) versus 58.3% (14/24) on control; risk difference -10.1 percentage points (95% CI -36.9 to 16.8), risk ratio 0.83 (0.50–1.37); unadjusted two-proportion z-test p = 0.465.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Early Vigabatrin and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary questions spanning seizure occurrence during the randomized phase, time to first clinical seizure, drug-resistant epilepsy, developmental and autism assessments, adverse events, and an EEG biomarker. The numerical result details available for several outcomes show estimates with considerable uncertainty, while the different measures address distinct clinical and developmental questions. Numerical results for the other listed secondary measures are not reported in the registry record.

These outcomes add context to the primary cognitive assessment but do not directly replace it. Seizure occurrence and time to an event measure seizure-related outcomes; drug-resistant epilepsy is a separate outcome; developmental and autism assessments measure other aspects of development. Their scales, follow-up summaries, and statistical methods differ. A result on one measure cannot be assumed to answer the primary question about Bayley cognitive scores.

The record does not report a multiplicity adjustment for the secondary analyses. In general, testing many outcomes creates more opportunities for a chance finding, even when none of the underlying effects is real. Unadjusted p-values therefore carry less confirmatory weight when considered across a set of outcomes. A nominally notable result should be interpreted alongside its uncertainty, the number and variety of outcomes examined, and whether the analysis was planned.

The secondary results are best read as exploratory or contextual unless the registry record establishes a confirmatory role and analysis plan. Such a plan, including any hierarchy or multiplicity procedure, is not reported in the registry record. This means the secondary findings can help describe the trial's observed outcome pattern, but they should not be treated as independent proof that resolves uncertainty in the primary comparison.

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

• Number of Subjects That Develop Seizures When Treated With Study Drug During the Randomized Phase of the Study.
• Time to the Subject's First Clinical Seizure From Randomization
• Count of Participants With Drug Resistant Epilepsy at 24 Months of Age.
• Evaluate Vineland II ABC Scores and Impact of Early Versus Late Treatment
• Evaluate Autism Diagnostic Observation Schedule 2nd Edition (ADOS2) Scores and Impact of Early Versus Late Treatment
• Number of Subjects With Vigabatrin Related Adverse Events and Severe Adverse Events
• EEG Biomarker for Developing Epilepsy

9. Statistical Interpretation

10. Statistical Methods Explained

For the primary endpoint, each group is described by its sample size, mean score, and standard deviation. The mean is the arithmetic average on the cognitive score scale. The standard deviation describes how dispersed participant scores are around that average; it is not a confidence interval for the mean and does not describe the full range of individual outcomes.

What does a mean difference describe?

A mean difference compares the average score in one group with the average score in another. The recalculated contrast is oriented as Early Vigabatrin relative to Delayed Vigabatrin, so its negative estimate indicates a lower posted mean in the early-treatment group. The confidence interval expresses uncertainty around that estimated contrast. The estimate alone does not show how precise the comparison is, and neither a mean difference nor a p-value establishes a causal explanation beyond the design and analysis supporting the comparison.

What is an unadjusted recalculation?

The recalculated results use the posted group summaries to form simple comparisons. They are unadjusted rather than model-based and are not a substitute for the trial's own analysis. Such calculations can help readers understand the direction and approximate uncertainty of a contrast, but they may not reproduce an analysis that accounts for the trial structure, covariates, missing outcomes, or other modeling choices. Details of those choices are not reported in the registry record unless stated in a reported analysis.

Why does the reported model matter?

The registry reports a Mixed Models Analysis for the randomized primary comparison, using a mean difference in final values. A mixed model is a general statistical approach that can represent dependence or structure in data, according to the model specified by investigators. The precise model specification, included covariates, and handling of missing scores are not reported in the registry record. Because the reported model and the simple recalculation are not identical analyses, their estimates and uncertainty can differ. Where the registry's sponsor analysis differs from the recalculation, the sponsor's own analysis takes precedence.

How should binary outcomes be read?

For outcomes such as developing seizures or drug-resistant epilepsy, the registry gives participant counts in each group. A risk difference describes the difference between the proportions with the outcome in the two groups. Ratios such as a risk ratio or odds ratio describe the contrast on a different scale. These are not interchangeable summaries, and interpretation should account for their confidence intervals and the number of participants observed. The posted recalculations are unadjusted; the registry's own analyses for these outcomes are listed as Chi-squared tests.

What does a time-to-event analysis add?

Time to first clinical seizure is a time-to-event outcome. A median time describes the point by which half of the observed event-time distribution has occurred, with the precise interpretation depending on the analysis and censoring. A Cox regression analysis compares event rates over follow-up through a hazard ratio. In general, a hazard ratio is not a difference in median times and does not directly state the probability that an individual will experience an event. The registry reports a Cox regression analysis for this outcome; further model details are not reported in the registry record.

Over-dispersion is a general issue for count data when variability exceeds what a simple count model expects; accounting for it can affect standard errors and intervals. The posted primary outcome is continuous rather than a count, and the registry does not report an over-dispersion analysis. More generally, model choice should follow the outcome type and trial design, and assumptions that are not described should not be inferred.

11. Confidence Intervals and Precision

The recalculated primary comparison between Early Vigabatrin and Delayed Vigabatrin has a 95% confidence interval from -12.07 to 6.068 score points. It spans zero, so the posted summaries are compatible with no mean difference as well as with differences in either direction. The interval is broad enough that the point estimate alone cannot be treated as a precise estimate of the underlying contrast.

In general, a confidence interval describes a range of values reasonably compatible with the data under the analysis assumptions. It does not mean there is a 95% probability that the true effect lies within this particular interval. Its width reflects statistical uncertainty, which can depend on sample size, variability, and the method used. The posted standard deviations show appreciable variation in cognitive scores within the groups, which is relevant to the precision of mean comparisons.

The unadjusted recalculation comparing Watchful Waiting with Delayed Vigabatrin has a 95% confidence interval from 1.164 to 25.64. Although this interval does not include zero, the comparison involves the Watchful Waiting group, defined by its observed course, rather than a randomized treatment arm. Statistical precision does not remove that design distinction or establish that the groups are comparable.

For secondary outcomes, the seizure risk-difference interval ranges from -0.281 to 0.199, and the drug-resistant epilepsy interval ranges from -0.369 to 0.168. The reported time-to-event hazard-ratio interval is 0.309 to 1.140. These intervals convey substantial uncertainty about the corresponding contrasts; their scales differ, so they should not be compared as if they measured the same quantity. The registry's own analyses should be preferred for the reported trial conclusions.

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 illustrations based on the observed effects, not the assumptions used to design the trial. The original trial's sample-size assumptions and justification are not reported in the registry record. The planning illustration uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It considers detecting the full observed effect and smaller fractions of that effect, including 75% and 50% of the observed effect.

For the continuous and binary outcomes, the figures are participants per arm. For the time-to-event outcome, they are total events, not participants per arm. The 80% power column describes a planning scenario in which the assumed effect would be detected at the stated significance level in 80% of repeated studies under the calculation's assumptions. The 90% power column uses a higher probability of detection under those same assumptions. These are design-planning quantities, not guarantees for a future study.

The smaller the effect a study aims to detect, the more participants or events the planning calculation requires. This follows because a smaller contrast is harder to distinguish from random variation. The numbers depend on the observed effect used as a starting point, so they should not be treated as a recommended sample size without a separate design decision about the effect that matters and the study assumptions.

This is not observed power. It does not describe the probability that the completed trial detected an effect after seeing its results, and it does not resolve uncertainty in the posted estimates. The planning values are illustrations only.

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 = -3.000; pooled standard deviation σ = 16.370.
2. n = 2 × (1.96 + 0.842)² × 16.370² / -3.000² = 467.4, rounded up to 468 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 <- -3                      # observed difference in means
sigma <- 16.3697648119941                     # 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(2849457)
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 = 468 (80% power), 626 (90% power)
 75% of observed effect: n per arm = 831 (80% power), 1,113 (90% power)
 50% of observed effect: n per arm = 1,870 (80% power), 2,503 (90% power)
power.t.test: 468.4 
Simulated power at n = 468 per arm: 0.804 (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 analysis is a Mixed Models Analysis comparing the randomized Delayed Vigabatrin and Early Vigabatrin groups. It reports a mean difference in final values with a 95% confidence interval and a p-value. The confidence interval spans zero, so the reported estimate is compatible with no difference as well as with differences in either direction.

The simple recalculation from the posted summary statistics gives a different estimate and uncertainty from the sponsor's model-based analysis. This is a discrepancy between analyses, not a reason to substitute the recalculation for the trial's reported result. The recalculation is unadjusted and based on group-level summaries, while the registry identifies the sponsor's method as mixed models. The registry record does not provide enough model detail to explain the numerical difference.

Accordingly, the sponsor's own analysis takes precedence when describing the trial's reported primary finding. The recalculation remains a secondary statistical check that helps illustrate how a simple comparison of the posted means behaves. It does not reproduce the sponsor's method, establish which modeling choices account for the discrepancy, or provide a basis for overriding the reported analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary outcome and multiple secondary outcomes, and it records several analyses. When many hypotheses are tested, the chance of at least one apparently notable result can increase. Statistical methods can address this through prespecified approaches such as controlling a family-wise error rate or organizing outcomes hierarchically. These are general options, not claims about what this trial did. A multiplicity adjustment or a formal hierarchy is not reported in the registry record.

Without a reported adjustment, unadjusted secondary p-values should be interpreted cautiously. The primary outcome remains the main endpoint specified in the record, but the precise analysis plan, including any prespecified handling of multiple testing, is not reported. The registry also does not report whether interim analyses were conducted or whether any stopping boundaries were used. Those features should not be inferred from the completed status.

The primary analysis population is described as intent to treat. The record states that three participants withdrew before 24 months of age and one participant did not complete the Bayley assessment at 24 months. It does not report how the missing primary scores were handled in the sponsor's mixed model, whether any imputation was used, or whether sensitivity analyses assessed the effect of missingness. These details matter because missing outcomes can affect both the estimated contrast and its uncertainty, depending on why data are missing and how the analysis treats them.

Group-specific denominators vary across posted outcomes, reflecting the outcome-specific records. The registry does not report a full accounting that links every missing observation to each analysis population or explains all denominator differences. Nor does it report detailed protocol deviations or the analysis population definitions for every secondary endpoint. These gaps limit independent assessment of the full analysis process and reinforce the need to distinguish the sponsor's reported analysis from unadjusted recalculations.

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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: nervous system disorders (50.0%), respiratory, thoracic and mediastinal disorders (13.8%), eye disorders (8.3%), infections and infestations (7.4%), cardiac disorders (3.7%).

The registry reports serious adverse events separately for pre-randomization and post-randomization periods, and it lists groups with risk counts and affected-participant counts. For example, the post-randomization delayed-placebo group lists 14 affected participants among 27 at risk for serious adverse events, and the early-treatment group lists 15 among 29. These are the posted counts, not estimates of treatment causation. The record also lists other adverse events separately, so the serious-event and other-event counts should not be combined.

The safety entries are organized across different treatment periods and groups, including open-label vigabatrin before and after starting treatment. Those groupings should be kept distinct when reading the counts. The record lists zero deaths in each adverse-event group. It also lists serious-event categories, with nervous system disorders at 50.0% and respiratory, thoracic and mediastinal disorders at 13.8%, among the top terms reported.

These entries describe events recorded in the registry; they do not by themselves establish whether an event was caused by treatment. The record does not provide enough detail to infer comparative event rates across all periods or to resolve differences in exposure and follow-up. Safety counts should therefore be interpreted as descriptive registry results rather than as causal estimates.

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

The posted primary results describe cognitive scores at 24 months in the randomized early- and delayed-treatment groups, along with a separate Watchful Waiting group. The sponsor's reported mixed-model comparison has an interval that spans zero. The simple recalculation also has an interval that spans zero, but its estimate differs from the sponsor's analysis. The sponsor analysis takes precedence for the reported primary result, while the recalculation illustrates the uncertainty in a basic comparison of posted summary statistics.

These results do not establish that the treatments are equivalent. A nonsignificant result is not proof that the underlying effects are identical, and a confidence interval spanning zero can include effects in either direction. Nor do the posted means alone establish that one treatment improves or worsens cognitive development. The study's group comparisons, uncertainty, analysis methods, and missing outcome information all matter to interpretation.

The higher mean in the Watchful Waiting group is not a randomized treatment contrast. That group was defined by not developing EEG abnormalities or clinical seizures during the study, whereas randomization followed detection of epileptiform activity. Comparing those groups descriptively does not establish what would have happened if participants had been assigned to one of the randomized treatments.

Secondary outcomes address seizure-related events and other developmental or safety questions. Their results add context but do not remove uncertainty in the primary endpoint, particularly because the record does not report a multiplicity plan and numerical details are absent for some listed outcomes. The findings should be understood as the results recorded for this trial and its analyses, not as a general conclusion beyond the participants, outcomes, and methods described.

18. Why This Trial Matters Statistically

This trial presents a useful statistical distinction between a randomized comparison and groups defined by events observed during follow-up. The randomized Early Vigabatrin and Delayed Vigabatrin arms form the primary treatment contrast. The Watchful Waiting group has a different role: participants remained in it if they did not develop the specified EEG or clinical signs. Its results can describe that group, but they should not be interpreted as if it were another randomly assigned treatment arm.

The trial also illustrates why a point estimate is not enough. The primary score difference is accompanied by uncertainty, and the sponsor's mixed-model estimate differs from a simple recalculation from the posted means and standard deviations. Reporting both the sponsor's analysis and a transparent recalculation makes the distinction between model-based inference and an unadjusted summary comparison important to readers. The sponsor analysis remains the reported trial analysis.

Finally, the record connects a developmental endpoint with seizure-related secondary outcomes and safety reporting. These measures address different questions and have different statistical forms. Careful interpretation requires keeping their roles separate, recognizing the potential implications of multiple unadjusted tests, and noting missing analysis details without filling them in by assumption. Those are broadly useful habits for reading clinical trial results.

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 features of this record limit how fully the results can be independently assessed. The randomized comparison began only after EEG epileptiform activity was detected, so conclusions from the randomized phase concern participants reaching that study condition. The record also describes Watchful Waiting participants who did not develop EEG abnormalities or clinical seizures; that group is defined by observed course and is not a randomized comparator. The open-label vigabatrin group is listed separately, which further means the descriptive groups should not be treated as a single randomized contrast.

The primary outcome has missing observations: three participants withdrew before 24 months of age, and one participant did not complete the Bayley assessment at 24 months. Although the record identifies an intent-to-treat analysis population, it does not report the specific missing-data method or sensitivity analyses. Details of the mixed model are also not reported, limiting comparison with the recalculated summary-statistic contrast.

The registry does not report the original sample-size justification, full analysis plan, multiplicity approach, interim-analysis procedures, or detailed handling of all outcome-specific denominators. Numerical results are not reported in the registry record for every listed secondary measure. The safety entries are divided across time periods and groups and do not establish causality. Together, these limitations counsel against treating any one point estimate or unadjusted secondary result as a complete account of the trial.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Preventing Epilepsy Using Vigabatrin In Infants With Tuberous Sclerosis Complex — NCT02849457.
• Registry record last updated 2024-08-19; status last verified 2024-07.
• Results first posted 2024-08-19.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes PREVeNT as a completed, randomized, double-blind, placebo-controlled phase IIb trial in infants with tuberous sclerosis complex. The listed enrollment is 84; the study summary describes a goal of 80. Randomization followed detection of epileptiform activity on EEG, comparing Early Vigabatrin with Delayed Vigabatrin.

The primary outcome was Bayley cognitive score at 24 months. The registry reports a mixed-model comparison for the randomized groups and group summary statistics that permit an unadjusted recalculation; these analyses differ, and the sponsor's analysis takes precedence. Secondary outcomes cover seizure-related, developmental, and safety measures. The record reports missing primary assessments and does not report several details needed to fully evaluate the analysis plan, missing-data handling, or multiplicity.