Adjunctive GNX Treatment Compared With Placebo in Children and Adults With TSC-related Epilepsy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Adjunctive GNX Treatment Compared With Placebo in Children and Adults With TSC-related Epilepsy (NCT05323734), a randomized phase 3 study. The primary outcome is Percent Change From Baseline in 28-day Seizure Frequency for Primary Seizure Type During Double Blind Period.

2. Clinical Question

This question concerns the difference between randomized groups in a defined seizure-frequency measure. The endpoint includes specified seizure types, including atonic/drop, bilateral clonic, bilateral tonic, focal motor seizures, focal to bilateral tonic-clonic seizures, and generalized tonic-clonic seizures. It does not describe every possible seizure outcome or every aspect of epilepsy.

The study enrolled 129 participants and is listed as completed. Its design was randomized, parallel-group, and placebo-controlled, with triple masking recorded in the trial information. The summary describes the treatment as adjunctive, so the comparison concerns adding GNX or matching placebo within the trial setting rather than comparing the study drugs as standalone treatments.

The clinical question is distinct from whether the observed data establish a definitive difference. The mean difference estimate and its confidence interval describe the direction and uncertainty of the comparison; they do not by themselves establish the cause of individual changes or determine clinical importance. The registry record does not report a threshold for a clinically important difference.

3. Trial Design

TrustTSC is listed as a Phase 3, randomized, parallel-group, placebo-controlled study of adjunctive ganaxolone in children and adults with TSC-related epilepsy. The registry record lists Marinus Pharmaceuticals as the sponsor and an enrollment of 129. The study status is completed. Its start date is 2022-04-01 and its primary completion date is 2024-09-09.

Participants were assigned to ganaxolone or matching placebo. The ganaxolone arm is described as an oral suspension taken three times a day; the placebo arm used a matching oral suspension on the same schedule. The registry classification records triple masking, while the study summary describes the trial as double-blind. These are the descriptions recorded for the trial; further details about which roles were masked are not reported in the registry record.

The study summary describes a 4-week prospective baseline phase, defined as the first 28 days following screening. The double-blind phase consisted of a 4-week titration period from Day 1 to Day 28 and a 12-week maintenance period from Day 29 to Week 16. The primary endpoint is described as percent change from baseline in 28-day frequency of primary seizure types during the double-blind period. Its listed timeframe is Baseline (Day 1), Day 28.

The primary outcome population is the intent-to-treat set of randomized participants who dosed and had at least one post-baseline efficacy assessment. This definition is narrower than all randomized participants because it includes the dosing and post-baseline assessment requirements. The group sizes posted for the primary outcome are 64 for ganaxolone and 65 for placebo.

Details of the original sample-size justification, the trial's planned statistical methods beyond the information described in the registry, interim analyses, and any prespecified decision thresholds are not reported in the registry record. The planning illustrations based on the observed effect should therefore not be mistaken for the original design rationale.

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.

Before assignment: A total of 129 participants were enrolled in the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) Set comprises of randomized participants who dosed and had at least one post-baseline efficacy assessment.

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: Safety Analysis Set comprised of all randomized participants who receive at least 1 dose of the investigational product (IP).

6. Primary Endpoint

The registry lists the primary outcome as Percent Change From Baseline in 28-day Seizure Frequency for Primary Seizure Type During Double Blind Period, measured over Baseline (Day 1), Day 28.

The primary endpoint is percent change from baseline in 28-day frequency of primary seizure types during the double-blind period. It combines a participant’s seizure counts for the specified primary types into a frequency standardized to a 28-day period. The registry description states that frequency was calculated by dividing the total number of seizures by the number of days with seizure data in the period and multiplying by 28.

For each participant, percent change was calculated by subtracting baseline 28-day seizure frequency from post-baseline 28-day seizure frequency, dividing by baseline frequency, and multiplying by 100. On this scale, a negative value indicates that the measured frequency was lower after baseline, while a positive value indicates that it was higher. The group-level mean is an average of participant-level changes; it does not imply that every participant changed in the same direction.

A standardized frequency measure allows comparisons across periods even when the amount of seizure diary information differs. The registry specifies the seizure types counted, which helps define the endpoint rather than treating all seizure events as interchangeable. Frequency is used because the trial question concerns change in seizure occurrence over time, but the endpoint is only one measure of the broader clinical condition.

The primary outcome is reported as a mean with standard deviation. The posted outcome data do not give confidence limits for each arm separately. The comparative mean difference and its interval provide the direct summary of the difference between the group means, with uncertainty around that estimate.

7. Results Posted in the Registry

• Ganaxolone: mean -7.50 versus 13.57 on control; difference -21.07 (95% CI -45.01 to 2.87), standardized effect d = -0.30; z-test p = 0.084.

8. Secondary Efficacy Endpoints

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

Number of Participants Who Were Considered as Treatment Responders During Double Blind Period

• 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:
  • Ganaxolone: 18.8% (12/64) versus 12.3% (8/65) on control; risk difference 6.4 percentage points (95% CI -6.0 to 18.9), risk ratio 1.52 (0.67–3.48); unadjusted two-proportion z-test p = 0.312.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ganaxolone and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists three secondary outcomes: treatment responders during the double-blind period, and responder counts on the Clinical Global Impression of Improvement scale as assessed by a parent or caregiver and by a clinician. Numeric results are posted for the treatment-responder outcome. Numeric results for the parent/caregiver and clinician CGI-I outcomes are not reported in the registry record.

The posted responder comparison is a separate binary outcome from the primary continuous seizure-frequency endpoint. A responder count reduces participant outcomes to whether a specified response criterion was met, whereas the primary endpoint compares mean percentage changes in frequency. The registry summary does not give the response criterion itself, so the clinical meaning and threshold behind the responder classification cannot be evaluated from the record alone.

Across the secondary outcomes, the available information is therefore incomplete: the treatment-responder result is reported, while the two CGI-I responder results are not. The responder result is not a substitute for the primary endpoint, and it should not be treated as confirmation or refutation of the primary comparison. Different outcomes can capture distinct aspects of participants’ experiences and can yield different estimates.

Secondary results generally carry less evidential weight when many outcomes are examined without a reported multiplicity strategy. Testing multiple outcomes increases the chance that at least one result may appear unusual under a null model. The registry record does not report whether the secondary analyses were adjusted for multiplicity, whether a testing hierarchy was prespecified, or whether the results were considered exploratory. Accordingly, secondary findings should be interpreted as supportive context, not as stand-alone proof of a treatment effect.

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

• Number of Participants Who Were Considered as Treatment Responders During Double Blind Period
• Number of Responders to Clinical Global Impression of Improvement (CGI-I) Scale as Assessed by Parent/Caregiver
• Number of Responders to Clinical Global Impression of Improvement (CGI-I) Scale as Assessed by Clinician

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean difference represent?

The primary outcome is a continuous measure: each participant’s percent change in 28-day seizure frequency. The posted group summaries report means and standard deviations. The recalculated mean difference is the ganaxolone group mean minus the matching-placebo group mean, on the percent-change scale. A negative estimate means the ganaxolone group mean was lower on that scale. It is a contrast between group averages, not a statement that every participant’s outcome followed that direction.

The recalculation is an unadjusted comparison based on the posted summary statistics. It does not incorporate participant-level covariates or a model adjustment. The registry record does not report a covariate-adjusted primary estimate. The comparison is therefore a simple summary of the two posted group means, and it may not reproduce a sponsor analysis that uses a different endpoint summary or statistical method.

Why might a rank-based analysis be used?

The sponsor’s reported primary analysis is a Wilcoxon Rank-Sum analysis and gives a median difference in final values. A rank-based procedure orders observations and compares their distributions using ranks, rather than relying directly on a difference between arithmetic means. In general, rank methods can be useful when data are skewed or contain influential extreme observations, although they answer a different statistical question from a mean comparison. The registry record does not state why this method was selected or describe the distributional rationale.

The reported analysis names median difference in final values, while the posted primary endpoint is percent change from baseline. That distinction matters: a mean difference in percent change and a median difference in final values are not interchangeable summaries. The reported method and estimate should be understood on their own terms, without treating the two numerical estimates as if they were generated from the same estimand.

What does the standard deviation tell us?

A standard deviation describes the spread of observations around a group mean. The posted standard deviations, 60.43 in the ganaxolone group and 77.37 in the placebo group, indicate substantial variability in the participant-level outcome. General statistical principle: when outcome variation is large relative to a group difference, the group comparison is less precise unless supported by sufficiently informative data. Variability also means that group means do not describe the experience of each individual participant.

The recalculated pooled standard deviation is 69.49. The standardized mean difference, -0.303, scales the mean difference by pooled variability. This dimensionless summary can help express the size of a continuous contrast relative to the spread in the data. It does not provide a clinical threshold, and it does not remove uncertainty about the estimate.

How should confidence intervals and p-values be read?

A confidence interval gives a range of estimates compatible with the data under the method’s assumptions and repeated-sampling framework. It communicates both the point estimate and its precision. The recalculated 95% interval runs from -45.01 to 2.867, so it includes zero. In general, an interval that includes zero for a difference is compatible with no group difference as well as with differences in either direction within the interval. The interval does not give the probability that the true effect lies inside its limits.

The unadjusted p-value for the recalculated mean comparison is 0.084. The sponsor’s rank-based analysis reports p = 0.090. These values are attached to different analyses. A p-value is calculated under a null hypothesis and analysis assumptions; it is not a measure of clinical importance or the probability that a finding is due to chance. The registry record does not state whether the reported p-values were adjusted for testing multiple outcomes or analyses.

Why can over-dispersion matter?

General statistical principle: over-dispersion means observations vary more than a model assumes. If a method assumes less variability than is present, its standard errors can be too small and its intervals too narrow. Conversely, an analysis that properly represents the observed variability can produce more cautious uncertainty estimates. The posted standard deviations show the scale of variation in the primary outcome, but the registry record does not characterize the data as over-dispersed or report a model-based dispersion assessment. No conclusion about a particular model’s adequacy should be inferred from the summary statistics alone.

What is not described about the analysis?

The registry record does not report the original sample-size justification, detailed missing-data procedures, handling of participants who discontinued or had incomplete seizure diaries, interim analyses, or a complete statistical analysis plan. It also does not report whether covariates were included in the sponsor’s analysis or describe prespecified sensitivity analyses. These omissions limit the ability to assess the full analysis process from the registry information alone. They do not prove that the trial lacked such procedures; they mean those details are not reported in the registry record.

11. Confidence Intervals and Precision

The recalculated primary mean difference is -21.07, with a 95% confidence interval from -45.01 to 2.867. The interval spans zero, so the posted summary statistics do not isolate the direction of the underlying group difference. Values across a fairly broad range remain compatible with the recalculation’s assumptions. The point estimate is one estimate among that range, not a precise measurement of the true difference.

Confidence intervals are a way to express statistical uncertainty. In general, a 95% confidence procedure is designed so that intervals constructed in the same way across repeated comparable studies would contain the true parameter 95% of the time, assuming the model and sampling process are appropriate. This does not mean there is a 95% probability that this particular interval contains the true effect. Nor does the interval indicate whether any possible difference is clinically important.

The sponsor’s reported rank-based analysis gives a median difference of -14.53, with a 95% confidence interval from -32.04 to 2.48. That interval also includes zero. Because it summarizes a median difference in final values, it should not be read as a second calculation of the same mean percent-change contrast. The two analyses nonetheless both convey uncertainty about the direction and magnitude of the comparison.

The primary outcome standard deviations are 60.43 for ganaxolone and 77.37 for placebo. Their size relative to the group estimates reflects substantial dispersion in participant outcomes. The recalculated standard error is 9.597 for placebo and 7.554 for ganaxolone; these are components of the uncertainty calculation, not measures of clinical variability in the same sense as the standard deviations.

Precision is also affected by the number of participants contributing to an outcome, the amount and pattern of missing information, and the statistical method. The registry record defines the primary population but does not report the missing-data procedures or all analysis details. Confidence intervals should therefore be interpreted as conditional on the recalculation method and its assumptions, not as a complete account of every possible source of uncertainty.

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 estimates are participants per arm, not total participants and not total events. They illustrate the sample size associated with detecting a stated fraction of the observed effect under the listed assumptions. The assumed design uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. For each line, the effect to detect is the stated fraction of the observed effect. These are planning illustrations calculated from the observed effect, not the trial’s original design assumptions.

The 80% power column gives the number of participants per arm that the planning calculation associates with an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column gives the corresponding per-arm number for a higher chance of detecting that same specified effect. These are design concepts, not guarantees that a future study will obtain a particular result.

For the primary continuous outcome, planning for 100% of the observed effect gives 171 participants per arm for 80% power and 229 participants per arm for 90% power. Planning for 75% of the observed effect gives 304 and 407 participants per arm, respectively. Planning for 50% of the observed effect gives 683 and 915 participants per arm, respectively. The smaller the effect targeted for detection, the more participants the calculation requires, because a smaller difference is harder to distinguish from random variation.

The displayed curve represents the same planning relationship across effect sizes: as the target effect becomes smaller, the required sample size rises. The calculation is not observed power. It does not describe the probability that the completed trial detected its observed result; observed-effect-based power is not a substitute for interpreting the estimate and confidence interval.

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 = -21.070; pooled standard deviation σ = 69.487.
2. n = 2 × (1.96 + 0.842)² × 69.487² / -21.070² = 170.7, rounded up to 171 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 <- -21.07                      # observed difference in means
sigma <- 69.4870715196572                     # 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(5323734)
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 = 171 (80% power), 229 (90% power)
 75% of observed effect: n per arm = 304 (80% power), 407 (90% power)
 50% of observed effect: n per arm = 683 (80% power), 915 (90% power)
power.t.test: 171.7 
Simulated power at n = 171 per arm: 0.795 (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 Wilcoxon Rank-Sum comparison of median difference in final values. It reports -14.53, with a 95% confidence interval from -32.04 to 2.48 and p = 0.090. The unadjusted recalculation from the posted group summary statistics instead compares means for percent change from baseline. It gives a mean difference of -21.07, a 95% confidence interval from -45.01 to 2.867, and p = 0.084.

These values are not competing estimates of exactly the same quantity: one is a rank-based reported analysis of median difference in final values, and the other is a simple unadjusted mean comparison for the percent-change outcome. Their point estimates should not be expected to match. Both confidence intervals include zero, and both analyses express uncertainty about the comparative result.

No discrepancy is flagged between the posted result and the recalculation. If a discrepancy were present, the sponsor’s own analysis would take precedence. The recalculation is best used as a transparent supplementary check based on summary statistics, not as a replacement for the sponsor’s reported method or a reconstruction of analyses requiring participant-level data.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome and three secondary outcomes. The secondary outcomes include a treatment-responder count and responder assessments on the CGI-I scale from parent/caregiver and clinician perspectives. The existence of several outcomes raises a general statistical issue: when many hypotheses are tested, the chance of at least one apparently unusual result can increase even if the treatments do not differ on any outcome.

Multiplicity can be handled in several ways, such as adjusting the significance threshold, specifying an ordered testing strategy, or identifying analyses as exploratory. These are general approaches; which, if any, was used for this trial is not reported in the registry record. A prespecified statistical analysis plan and any multiplicity procedure are not described in the registry information. The posted unadjusted p-values should therefore be read as unadjusted, not as evidence that a family-wise error rate was controlled.

Missing-data handling is also important for a seizure-frequency endpoint, which depends on recorded seizures and days with seizure data. The endpoint description explains how frequency was standardized to 28 days, but the registry record does not report how missing diary days, incomplete periods, discontinuations, or other unavailable outcomes were handled in the analysis. It also does not describe imputation, sensitivity analyses, or assumptions about why observations might be missing. Standardizing frequency by observed diary days does not, by itself, explain the treatment of missing information.

The primary analysis population is defined as randomized participants who dosed and had at least one post-baseline efficacy assessment. This definition clarifies who contributed to the stated primary analysis, but it does not provide a full account of participants excluded from that set or the reasons for their absence. The registry record does not report additional analysis populations or how results differed across them.

These gaps limit assessment of robustness, not necessarily the validity of the trial. They mean readers cannot determine from the registry record alone how multiplicity, missing outcomes, or alternative analysis populations may have affected the conclusions. Those details would be needed for a fuller assessment of the analysis plan and its implementation.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: erysipelas (1.6%), influenza (1.6%), pneumonia (1.6%), pneumonia aspiration (1.6%), seizure (1.6%).

The posted safety figures list serious adverse events among 5 participants at risk in the ganaxolone group and 6 participants at risk in the matching-placebo group. The corresponding groups at risk are 64 and 65. The record lists zero deaths in each group. These are counts from the trial record; they do not by themselves establish whether an event was caused by study treatment.

The registry also lists serious-event terms with percentages: Erysipelas, Influenza, Pneumonia, Pneumonia Aspiration, and Seizure at 1.6% each, and Cellulitis at 1.5%. The percentages are presented as recorded and should not be added together or treated as mutually exclusive without information about how the event categories were counted. The registry record does not report further details about event timing, severity beyond the serious classification, or causal assessment.

Serious adverse event counts are different from all adverse events, and they are not an efficacy measure. Differences in counts between groups should be interpreted in light of the group sizes and the trial’s limited observation period. These summary figures are not a complete account of safety, and they do not support conclusions about risk beyond the data recorded for this study.

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

The primary result is a comparison of mean percent change from baseline in 28-day frequency of specified seizure types. The observed group means were -7.5 for ganaxolone and 13.57 for matching placebo. The recalculated mean difference was -21.07, with a 95% confidence interval from -45.01 to 2.867. This estimate points toward a lower mean percent change in the ganaxolone group, but its interval includes zero and allows for differences in either direction.

The result therefore does not precisely determine the size or direction of the underlying group difference. The sponsor’s reported rank-based result also has a confidence interval that includes zero, but it summarizes a different quantity. Neither summary should be reduced to a simple claim that the treatment was effective or ineffective. The registry results describe estimates and uncertainty; they do not establish a definitive clinical conclusion.

The endpoint measures frequency change for specified primary seizure types, not every seizure type or every dimension of TSC-related epilepsy. The posted group averages also do not describe each participant’s response. The substantial standard deviations signal considerable variation in outcomes, while the registry record does not provide a clinical-importance threshold by which to judge the magnitude of a difference.

The trial’s population, treatment schedule, analysis population, and observation period define the scope of what the data address. Generalization beyond this randomized study requires considering whether other populations, clinical settings, or treatment conditions are comparable. The registry record does not establish that the findings apply to all people with TSC or all epilepsy treatment contexts.

Finally, statistical uncertainty and clinical meaning are related but distinct. A confidence interval describes uncertainty in a group contrast under analysis assumptions; it does not determine whether a possible difference matters to patients. The posted results can inform understanding of the trial comparison, but decisions about care require evidence and context beyond these registry summaries.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate should be interpreted together with its uncertainty. The recalculated mean difference is -21.07, but its 95% confidence interval extends from -45.01 to 2.867. The point estimate alone may look more conclusive than the full interval warrants. The interval makes clear that the data do not settle the direction and magnitude of the comparison with precision.

It also demonstrates that analyses can summarize related outcomes differently. The recalculation compares group means for percent change from baseline, while the sponsor reports a Wilcoxon Rank-Sum analysis of median difference in final values. Those methods target different summaries and are not expected to produce identical estimates. Statistical interpretation depends on understanding what each estimate represents, not merely comparing the numbers.

The primary endpoint is a transformed frequency measure that accounts for the number of days with seizure data. Its interpretation depends on the defined seizure types and the observation periods used. That offers a clear framework for comparison, while also underscoring the importance of knowing how incomplete diary information was handled. Such missing-data details are not reported in the registry record.

The sample-size illustrations show how design requirements depend on the effect one hopes to detect. Smaller targeted effects require more participants under the stated planning assumptions. This is a useful planning principle, but the illustrations are based on the observed effect and do not reveal the trial’s original design rationale or observed power.

Finally, this record places primary, secondary, and safety information in a randomized placebo-controlled context while leaving several analytical details unreported. Recognizing both what the summaries show and what the registry does not describe is central to a balanced statistical reading.

19. Limitations

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

The primary recalculation relies on group summary statistics rather than participant-level data. It cannot reproduce analyses that require individual observations, covariate adjustment, stratification, or detailed handling of repeated measurements. The registry record does not report a complete analysis plan or covariate strategy, so the recalculation should be viewed as a simple unadjusted comparison.

The primary endpoint is defined using selected seizure types and a 28-day frequency standardization. The record does not provide participant-level distributions, the prevalence of extreme percentage changes, or details about how baseline values of zero, if any, were addressed. These issues may be relevant when interpreting a percent-change endpoint, but their occurrence and handling are not reported in the registry record.

There is a distinction between the primary endpoint description and the sponsor’s reported analysis summary: the endpoint is percent change from baseline, whereas the reported Wilcoxon result is described as median difference in final values. Without further analysis documentation, the relationship between those summaries cannot be fully assessed. They should not be treated as identical estimands.

The registry does not report missing-data procedures, discontinuation handling, sensitivity analyses, detailed multiplicity control, interim analyses, or the original sample-size justification. The primary analysis population is defined, but the record does not provide a full participant flow or explain differences between that population and everyone randomized. These omissions limit evaluation of robustness and possible selection effects.

Numeric results for the two CGI-I secondary outcomes are not reported in the registry record, and the treatment-responder criterion is not described in the outcome text. The safety summary gives event counts and selected terms but does not provide a complete account of timing or causal attribution. These limitations mean the registry summaries alone cannot answer every question about efficacy, safety, or analysis choices.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Adjunctive GNX Treatment Compared With Placebo in Children and Adults With TSC-related Epilepsy — NCT05323734.
• Registry record last updated 2025-07-11; status last verified 2025-06.
• Results first posted 2025-07-11.
• 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.

23. Record Summary

NCT05323734 is the completed Phase 3 TrustTSC randomized, parallel-group, placebo-controlled trial of adjunctive ganaxolone in children and adults with TSC-related epilepsy. Enrollment was 129. The double-blind phase included titration and maintenance periods, following a prospective baseline phase.

The primary outcome was percent change from baseline in 28-day frequency of primary seizure types. The posted group means were -7.5 for ganaxolone and 13.57 for matching placebo. The unadjusted recalculated mean difference was -21.07, with a 95% confidence interval from -45.01 to 2.867. The sponsor reported a Wilcoxon Rank-Sum median difference in final values of -14.53, with a 95% confidence interval from -32.04 to 2.48.

The record lists three secondary outcomes, but numeric results are not reported for the two CGI-I responder outcomes. Serious adverse events were recorded for 5 ganaxolone participants and 6 placebo participants, with zero deaths in each group. Important analysis details, including missing-data handling, multiplicity procedures, and the original sample-size justification, are not reported in the registry record.