Ganaxolone Treatment in Children With Fragile X Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ganaxolone Treatment in Children With Fragile X Syndrome (NCT01725152), a randomized phase 2 study. The primary outcome is Clinical Global Impression-Improvement (CGI-I) Scale.

2. Clinical Question

The study was registered as a Phase 2 proof-of-concept trial intended to assess safety, tolerability and efficacy related to anxiety and attention in children with Fragile X Syndrome. Its primary outcome was the CGI-I score at the end of treatment. The registry record gives the treatment sequences and outcome summaries, but does not report the original sample-size justification or full statistical analysis plan.

3. Trial Design

This was a randomized, quadruple-masked, placebo-controlled crossover trial, listed as Phase 2 and completed in the registry. Enrollment was 59. Participants were assigned to one of two sequences: ganaxolone followed by placebo, or placebo followed by ganaxolone. A crossover design differs from a parallel-group design because participants receive treatments in sequence rather than remaining in only one assigned treatment group.

The record describes a 2-week titration toward 12 mg/kg three times daily and a further 4 weeks at that dose. A 2-week washout separated the treatment periods. For the placebo-first sequence, the record describes ganaxolone for 6 weeks, from week 8 to 14. The description of the placebo period in the other sequence is incomplete in the registry record, so its full duration is not reported in the registry record.

The primary outcome was assessed at week 14, at the end of treatment. The reported outcome summaries include 52 participants for ganaxolone and 54 for placebo; these are the available outcome counts in the posted results, not a statement that each sequence had those numbers. In a crossover trial, treatment comparisons can depend on how within-participant data and treatment periods are handled. The sponsor-reported analysis is identified as a linear mixed-effect analysis, but its model specification and assumptions are not reported in the registry record.

The record also lists five secondary outcome measures, including anxiety, mood, behavior and attention scales. The trial is marked completed. The registry record does not report the original design assumptions, the planned handling of period or carryover effects, or a detailed account of masking procedures.

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: 59 participants were randomized in the study.

Treatment Period 1 (Week 1 to Week 6)

Reasons for not completing this period:

Washout Period (2 Weeks)

Treatment Period 2 (Week 8 to Week 14)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention-to-Treat (ITT) Population consisted of all participants who received medication and who had at least one post-Baseline assessment. Only those participants with data available at the specified data points 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.

Population: Safety Set included all participants who have taken at least one dose of study drug in Treatment period 1.

6. Primary Endpoint

The registry lists the primary outcome as Clinical Global Impression-Improvement (CGI-I) Scale, measured over Week 14 (End of Treatment).

The primary endpoint was the Clinical Global Impression-Improvement (CGI-I) Scale at week 14, the end of treatment. This clinician-rated scale assesses how much a participant’s illness has improved or worsened relative to the baseline state. Its seven ordered response categories range from very much improved to very much worse, with no change in the middle. Higher scores indicate a worse condition.

The CGI-I is used to summarize a clinician’s overall judgment of change rather than a single symptom or behavior. That broad assessment can be useful when the clinical question concerns overall improvement, but it also means the result is a rating on an ordered scale. The registry reports least-squares means and standard errors for the treatment groups. Those summaries describe the posted group results; they do not show how individual participants changed or how consistently clinicians rated them.

For the primary outcome population, the record includes participants who received medication and had at least one post-baseline assessment. It further states that only participants with data available at the specified assessment points were analyzed. The details of how unavailable assessments were handled beyond this description are not reported in the registry record.

7. Results Posted in the Registry

• Ganaxolone: mean 3.40 versus 3.50 on control; difference -0.10 (95% CI -0.46 to 0.26), standardized effect d = -0.11; z-test p = 0.586.

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.

Pediatric Anxiety Rating Scale (PARS) Total Score

• 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 errors.
• Result:
  • Ganaxolone: mean 8.30 versus 9.20 on control; difference -0.90 (95% CI -2.40 to 0.60), standardized effect d = -0.23; z-test p = 0.239.
• 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 secondary measures covering anxiety, mood, behavior and attention, including PARS, VAS, ADAMS, ABC and SNAP-IV. The posted secondary outcome detail includes a PARS comparison. Results for the other listed measures are not reported in the registry record, so the overall pattern across all secondary endpoints cannot be determined from the available outcome details.

The available PARS comparison does not provide a clearly separated treatment estimate in its unadjusted recalculation: its confidence interval crosses zero. This is broadly consistent with caution about interpreting the primary result as evidence of a distinct treatment contrast, but it cannot establish that all secondary measures followed the same pattern. The scales assess different aspects of anxiety, mood, behavior and attention, and their results should not be treated as interchangeable.

Secondary analyses generally carry less weight than the prespecified primary analysis when many outcomes are examined. In general, testing multiple outcomes increases the chance that at least one appears notable by chance. Adjustments for multiplicity can address that issue, but whether any adjustment was planned or applied is not reported in the registry record. The secondary result should therefore be regarded as exploratory rather than as independent confirmation of the primary finding.

The record’s listing of several secondary outcomes does not reveal which were analyzed, how missing observations were handled for each measure, or whether a hierarchy of outcomes was specified. Those details are not reported in the registry record. The unreported results should not be inferred from the outcome names or from the available PARS result.

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

• Pediatric Anxiety Rating Scale (PARS) Total Score
• Visual Analogue Scale (VAS)
• Anxiety, Depression, and Mood Scale (ADAMS)
• Aberrant Behavior Checklist (ABC)
• Swanson, Nolan, and Pelham-IV Questionnaire (SNAP-IV)

9. Statistical Interpretation

10. Statistical Methods Explained

In general, a treatment-effect estimate describes the direction and size of an observed contrast between treatment conditions. For the primary outcome, the posted comparison is expressed as a mean difference, with ganaxolone subtracted from placebo. A negative estimate means the posted ganaxolone mean is lower. Since the CGI-I scale assigns worse condition to higher scores, a lower score points toward less worsening or greater improvement on the scale, but the estimate alone does not establish a meaningful clinical effect.

What does a least-squares mean represent?

In general, a least-squares mean is a model-based estimate of a group mean. It can differ from a raw arithmetic mean because it may reflect adjustment for terms in the fitted model. The registry identifies the primary outcome parameter as a least-squares mean, but does not give enough detail to identify all model terms or reproduce those estimates. The accompanying standard error describes uncertainty in an estimated mean; it is not the spread of individual participant scores.

Why can a crossover comparison need a mixed-effect model?

In general, crossover observations are linked because a participant contributes data under more than one treatment condition. A mixed-effect model can represent this dependence by including participant-level structure, alongside treatment and other model terms. Whether the analysis also models period, sequence, baseline measures or carryover depends on the specified model. The registry reports a linear mixed-effect analysis but does not report its full specification, so those details cannot be assumed.

In general, crossover trials can be efficient because each participant can contribute information under both conditions. They also rely on design and analysis considerations that are less prominent in a parallel-group comparison, such as whether treatment effects vary by period and whether effects persist into the next period. The record specifies a washout period, but the adequacy of that washout and any formal assessment of carryover are not reported in the registry record.

What does the simple recalculation add?

The recalculated comparison uses posted group means and standard errors to form an unadjusted mean difference and confidence interval. It offers a transparent summary derived from the posted statistics, but it is not a reconstruction of the sponsor’s mixed-effect model. The posted standard errors were also used to approximate the standard deviations for the recalculation, so it should be read as an approximate, unadjusted comparison. It does not account for the within-participant structure of the crossover unless that structure is represented in the underlying summary statistics, which is not established by the record.

A p-value summarizes how unusual data at least as incompatible with a specified null hypothesis would be under the model and assumptions used. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. A p-value from a simple recalculation and one from a mixed-effect model can differ because they use different methods and assumptions. The registry does not report sufficient detail to explain the numerical difference between those results.

Why does over-dispersion matter in general?

For count outcomes, over-dispersion means that variability exceeds what a simple model assumes. If it is ignored, standard errors can be too small and confidence intervals too narrow. This general issue is not central to the primary endpoint here, which is a continuous score summarized with means and standard errors. The posted record does not identify a count-outcome analysis for the primary result.

Finally, statistical significance and clinical importance are distinct. In general, a result can be estimated precisely but be too small to matter clinically, or be uncertain despite a potentially meaningful estimate. The registry does not report a threshold for a clinically important CGI-I difference, so the posted mean contrast cannot be classified against such a threshold.

11. Confidence Intervals and Precision

The recalculated primary confidence interval extends from the negative side to the positive side of zero. This means the summary data do not pin down a single direction for the treatment contrast: values compatible with the interval include a lower mean score with ganaxolone, a higher mean score, and no difference. The interval is therefore important context for the point estimate of -0.1, which alone would conceal the uncertainty around that estimate.

A confidence interval is, in general, a range generated by a statistical procedure that reflects uncertainty in an estimate under the method’s assumptions. It is not a range containing a specified proportion of individual participant scores. Nor does an interval crossing zero prove that the treatments have the same effect. Establishing equivalence would require a prespecified equivalence margin and an analysis designed to assess it; such details are not reported in the registry record.

The group standard errors for the primary least-squares means are 0.13 for ganaxolone and 0.13 for placebo. These quantify uncertainty in the estimated means, not participant-to-participant variability. The recalculated interval is based on an approximate, unadjusted method using posted summary statistics. It does not replace the sponsor’s mixed-effect analysis, whose full model details are not reported.

For the secondary PARS result, the recalculated confidence interval also crosses zero. This indicates uncertainty about the direction of that unadjusted contrast as well. Precision should be interpreted alongside the design, analysis method and limited registry detail, not from the point estimate or p-value alone.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. The original sample-size justification is not reported in the registry record. The planning calculation assumes a two-sided significance level of 0.05, equal allocation between two arms and a normal approximation. It considers the stated fraction of the observed effect as the effect to detect.

The figures are participants per arm, not total participants and not total events. The primary outcome illustration gives 1,407 participants per arm for 80% power when planning for 100% of the observed effect; for 90% power at that effect, it gives 1,883 participants per arm. The other rows show planning for 75% and 50% of the observed effect. The corresponding figures increase as the target effect becomes smaller.

In plain language, 80% power means that, if the assumed effect and model assumptions were correct, a study of the indicated size would have an 80% chance of detecting an effect at the specified significance threshold. The 90% column uses a higher target chance of detection, which generally requires more participants. Smaller effects are harder to distinguish from random variation, so they require more participants under the same planning assumptions.

These figures are not observed power. They are hypothetical planning outputs derived from the posted estimate. Because the observed effect is itself uncertain and the calculation uses simplified assumptions, the figures should not be read as a recommendation or as proof that the original trial was designed to enroll a particular number.

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 = -0.100; pooled standard deviation σ = 0.947.
2. n = 2 × (1.96 + 0.842)² × 0.947² / -0.100² = 1,406.6, rounded up to 1,407 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 <- -0.1                      # observed difference in means
sigma <- 0.946585970739055                     # 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(1725152)
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 = 1,407 (80% power), 1,883 (90% power)
 75% of observed effect: n per arm = 2,501 (80% power), 3,348 (90% power)
 50% of observed effect: n per arm = 5,627 (80% power), 7,532 (90% power)
power.t.test: 1407.5 
Simulated power at n = 1,407 per arm: 0.796 (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 registry identifies the sponsor’s primary comparison as a linear mixed-effect analysis and reports a p-value for that analysis. This is the trial’s own reported inferential result. The registry does not provide the model specification, coefficient estimate, confidence interval or enough detail to reproduce the analysis.

The recalculation is a separate, simple unadjusted comparison based on posted group means and standard errors. It gives a mean difference of -0.1 and an unadjusted p-value of 0.586. Its assumptions and treatment of the crossover structure differ from those of a potentially model-based analysis. The sponsor’s reported p-value is not identical to the recalculated p-value; that difference alone does not show an error, because the methods are not the same.

The registry discrepancy flag is false. The recalculation should therefore be read as a supplementary check on the posted summary statistics, not as a replacement for the sponsor’s analysis. Without the full mixed-effect model and its estimated treatment contrast, the reason for the difference cannot be established from the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists five secondary outcome measures, but it does not report a multiplicity adjustment, a testing hierarchy or a prespecified strategy for interpreting the secondary comparisons. In general, when many outcomes are tested, the chance of at least one apparently unusual result can increase. Adjustment procedures or a planned hierarchy can help control this issue. Without reported details, the secondary results should be interpreted cautiously, and the available result should not be treated as confirmatory evidence on its own.

The primary outcome population is described as participants who received medication and had at least one post-baseline assessment. The registry further states that only those with data available at the specified data points were analyzed. This identifies a modified availability condition, but the record does not explain how missing outcome values were handled, whether any imputation was used, or how many participants lacked particular assessments. Those details are not reported in the registry record.

The trial is a crossover study, so missing data in one treatment period can affect a participant’s contribution to the within-participant comparison. The registry does not report whether participants with incomplete crossover data contributed to the mixed-effect analysis, or how the model handled incomplete records. It also does not report analyses comparing included participants with those lacking data.

The sponsor analysis is described as linear mixed-effect, but the model terms and assumptions are not reported in the registry record. The registry also does not report whether interim analyses were planned or conducted. No conclusions about those procedures can be drawn from the posted information.

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 non-serious adverse event terms

For serious adverse events, the registry reports zero affected participants in the ganaxolone group among 59 at risk and zero affected participants in the placebo group among 54 at risk. It also reports zero deaths in each group. These are the posted counts for the reported safety groupings; they do not establish that no other adverse events occurred.

The record reports other adverse events for 49 participants in the ganaxolone group and 46 in the placebo group. Serious events and other adverse events are separate categories in the registry data, so the other-event counts should not be read as serious-event counts. The registry does not provide serious adverse event terms in the posted serious-event listing.

These figures describe the events recorded during the trial and do not by themselves establish comparative safety. In a crossover study, treatment exposure occurs in sequence, and interpretation of group-level safety counts depends on the record’s definitions and reporting periods. Detailed event descriptions, severity, timing and treatment-period attribution are not reported in the registry record.

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

The posted primary outcome means are close: 3.4 for ganaxolone and 3.5 for placebo, on a scale where higher scores indicate a worse condition. The recalculated mean difference is -0.1, and its confidence interval crosses zero. Taken together, these summaries do not identify a clear difference between the treatment conditions at week 14. The sponsor’s mixed-effect analysis also does not supply evidence of a clearly distinct result in the posted record, although the full model output is not reported.

This does not establish that ganaxolone and placebo have identical effects. A result that is uncertain can reflect a small effect, variability, limitations in the available data, or some combination of these. The confidence interval expresses uncertainty in the estimate, while the registry’s outcome summaries do not show the distribution of individual responses. No equivalence margin or non-inferiority framework is reported.

The results also do not establish effects on every aspect of anxiety, attention, mood or behavior. The registry lists several secondary measures, but the results for most of them are not reported in the registry record. One available secondary comparison cannot stand in for all of these domains, particularly when the measures assess different constructs.

The findings are specific to the trial population, design, assessment schedule and reported analysis. The record describes children with Fragile X Syndrome, a crossover treatment sequence and a week 14 primary assessment. It does not provide enough information to assess all modeling choices, missing-data assumptions or the clinical importance of a given CGI-I difference. The statistics describe the posted trial results; they do not, by themselves, justify a treatment decision.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate should be read together with its uncertainty. The primary mean difference is -0.1, but the recalculated confidence interval crosses zero. The direction of a point estimate is not enough to establish that a treatment contrast is distinct from no difference, and a p-value alone does not convey the range of plausible effects.

It also highlights the distinction between a sponsor’s prespecified or model-based analysis and a simple recalculation from summary statistics. The registry identifies a linear mixed-effect analysis for the primary comparison, while the recalculation uses posted means and standard errors. These analyses answer related but not identical statistical questions. Understanding the model matters especially in crossover designs, where observations from the same participant are related.

The record makes visible several uncertainties that matter to interpretation: full mixed-effect model details are not reported, the handling of missing assessments is not described beyond the analysis-population definition, and multiplicity procedures for secondary outcomes are not reported. These are not merely technical details; they shape how confidently results can be interpreted and how broadly they can be generalized.

Finally, the planning illustrations show how assumptions about the target effect influence the scale of a future study. They are hypothetical calculations based on the observed effect, not a reconstruction of the original design. Their role is to illustrate the relationship between effect size, power and participant numbers, not to retrospectively judge the trial’s design.

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 available registry record leaves important analysis details unspecified. Although the primary analysis is identified as linear mixed-effect, the fitted terms, covariance structure and handling of treatment period, sequence or carryover are not reported in the registry record. These details are especially relevant in a crossover trial, where measurements from one participant across treatment periods are related.

The primary endpoint summaries are least-squares means with standard errors, but the complete model output is not reported. The recalculation is unadjusted and approximate, so it cannot reproduce the sponsor’s analysis or account for unreported model structure. The outcome is an ordered rating scale, while the posted summaries use means; the registry does not provide response-category distributions that would help show how participants’ ratings were distributed.

The analysis population includes participants with medication exposure and at least one post-baseline assessment, with only available observations at specified assessment points analyzed. The number and pattern of missing assessments, imputation procedures and sensitivity analyses are not reported in the registry record. The placebo duration description for the ganaxolone-first sequence is incomplete, and the detailed safety event terms are not posted.

Although several secondary scales are listed, results for most are not reported in the registry record, and multiplicity handling is not described. The record also does not report a clinically important difference threshold for the primary scale. These gaps limit conclusions about the robustness, clinical importance and breadth of the findings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Ganaxolone Treatment in Children With Fragile X Syndrome — NCT01725152.
• Registry record last updated 2023-04-10; status last verified 2023-03.
• Results first posted 2023-04-10.
• 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

NCT01725152 is a completed Phase 2 randomized, quadruple-masked, placebo-controlled crossover trial of ganaxolone in children with Fragile X Syndrome. Enrollment was 59. Participants received ganaxolone and placebo in different sequences, with titration and a washout period described in the registry record.

The primary outcome was the CGI-I score at week 14. Posted least-squares means were 3.4 for ganaxolone and 3.5 for placebo. The sponsor’s analysis is identified as linear mixed-effect, while the supplementary unadjusted recalculation gives a mean difference of -0.1 with a confidence interval crossing zero.

The registry lists secondary measures related to anxiety, mood, behavior and attention. Most secondary results and several analysis details, including missing-data and multiplicity procedures, are not reported in the registry record. The posted statistics support cautious interpretation of the estimated treatment contrast and do not, alone, establish clinical benefit or equivalence.