Safety, Tolerability and Efficacy Study of STX209 in Subjects With Fragile X Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety, Tolerability and Efficacy Study of STX209 in Subjects With Fragile X Syndrome (NCT00788073), a randomized phase 2 study. The primary outcome is Aberrant Behavior Checklist Irritability Subscore.

2. Clinical Question

The trial asked whether STX209 could improve irritability and other problem behaviors associated with Fragile X Syndrome, and whether it was safe and tolerable. The primary outcome was the Aberrant Behavior Checklist Irritability Subscore, assessed after 4 weeks of treatment. The registry describes a randomized, quadruple-masked crossover comparison of STX209 and placebo.

Because the design is crossover, the registry’s group labels, STX209:Placebo and Placebo:STX209, indicate treatment order. They are not simply labels for separate groups receiving only one treatment. The record does not report the period-specific results, sequence effects, or details of how results from the two treatment periods were combined in the primary comparison.

3. Trial Design

This was a Phase 2, randomized, quadruple-masked, placebo-controlled crossover study. Its title describes a flexible-dose evaluation of STX209 for irritability in subjects with Fragile X Syndrome. The registry lists the study as completed, with a start date of 2008-11 and primary completion in 2010-03. Enrollment is listed as 63.

Participants were assigned to one of two treatment sequences: STX209 followed by placebo, or placebo followed by STX209. Each treatment period is described as 4 weeks. STX209 was given orally in capsules at a variable dose from 1mg bid to 10mg tid. Placebo was given orally in capsules using a matching flexible-dose titration protocol, bid to tid. The registry does not report the interval, if any, between treatment periods or the details of dose adjustment.

The crossover structure means that treatment order is relevant to interpretation: each sequence represents a different order of the two interventions. The listed n of 63 for each sequence should not be read as evidence that the study had separate, independent treatment groups of that size; the record does not provide enough information to describe participant flow or the analysis population in detail.

The primary outcome was the Aberrant Behavior Checklist Irritability Subscore after 4 weeks of treatment. The record describes the primary outcome measure as a least-squares mean with standard error. It does not report the protocol’s original sample-size assumptions, the rationale for its enrollment target, or details of interim analyses. Those design details 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.

STX209 Then Placebo

Reasons for not completing this period:

Placebo Then STX209

Reasons for not completing this period:

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 Aberrant Behavior Checklist Irritability Subscore, measured over After 4 weeks of treatment.

The primary endpoint was the Aberrant Behavior Checklist Irritability Subscore, measured in points on a scale after 4 weeks of treatment. The registry describes the Aberrant Behavior Checklist-Community Edition as a 58-item questionnaire completed by a parent or caregiver. It contains five independent subscales; the Irritability Subscore is one of them and comprises 15 items. The described score ranges from 0 to 45, with a decreased score indicating fewer aberrant behaviors and clinical improvement.

The registry says the full assessment was administered at baseline and at the end of each intervention period. A caregiver-reported measure can capture observed behavior in the participant’s usual context, which is relevant when irritability is the target outcome. As a continuous measure, the score can be summarized by a mean and compared between treatment sequences or periods. A mean difference describes the direction and size of a group-level contrast, while its uncertainty indicates how precisely that contrast is estimated.

The posted primary results identify least-squares means and standard errors for the sequence labels, but do not provide period-specific score summaries or an explanation of the model’s adjustment terms. The registry’s description of the endpoint does not itself establish whether the posted values represent change from baseline or final scores; the reported analysis is labeled as a comparison of final values.

7. Results Posted in the Registry

• Placebo:STX209: mean -5.30 versus -5.10 on control; difference -0.20 (95% CI -2.83 to 2.43), standardized effect d = -0.03; z-test p = 0.882.

8. Statistical Interpretation

9. Statistical Methods Explained

The posted primary outcome is continuous: it is measured in points, and the registry describes the summary as a least-squares mean. A mean gives a central summary of scores. A least-squares mean is a model-based mean, potentially adjusted for terms in a statistical model. Which terms were included in the sponsor’s model is not reported in the registry record, so the exact adjustment represented by that label cannot be reconstructed from the posted information alone.

The registry reports a standard error of 0.95 for each sequence summary. A standard error describes the estimated uncertainty of a statistic, such as a mean. It is not the same as the spread of individual participant scores: the standard deviation describes variation among observations, while the standard error describes uncertainty in an estimated summary. The unadjusted recalculation uses the posted standard errors and an approximated pooled standard deviation. Because that standard deviation is approximate, the recalculation should be understood as a summary-statistic calculation rather than a reconstruction of the sponsor’s full analysis.

The recalculated contrast is a mean difference of -0.2, with a confidence interval from -2.833 to 2.433 and an unadjusted p-value of 0.882. A confidence interval conveys uncertainty about the contrast under the calculation’s assumptions. The p-value measures how surprising a result at least as inconsistent with a null hypothesis would be under that hypothesis and the statistical model used. It is not the probability that the null hypothesis is true, nor does it measure the probability that a treatment is beneficial. The p-value belongs to the unadjusted recalculation; it is not the p-value from the sponsor’s ANCOVA.

The registry identifies the sponsor’s method as ANCOVA, or analysis of covariance, and labels the parameter as mean difference in final values. In general, ANCOVA compares outcomes while accounting for specified covariates. Such adjustment can change an estimated comparison or its uncertainty relative to an unadjusted calculation. The covariates, model form, handling of the crossover structure, and other analysis details are not reported in the registry record. For that reason, it is not possible to reproduce the sponsor’s analysis or attribute the discrepancy to a specific model feature.

Why does the crossover design matter?

In a crossover study, treatment order matters because participants are assigned to sequences that receive both interventions in different orders. The posted sequence summaries do not, by themselves, show the separate treatment-period results or how within-participant information was used. General statistical practice for crossover data distinguishes treatment effects from period and sequence effects and considers whether effects from one period could persist into another. The registry does not report those analyses or whether carryover was assessed. It would therefore be inappropriate to infer that these issues were either present or absent.

Why can over-dispersion matter?

Over-dispersion is a general concern when observed variability exceeds what a statistical model assumes. If variability is understated, standard errors and confidence intervals can be too small, making results appear more precise than they are. This concept is most directly relevant to models for counts or other outcomes with a specified mean-variance relationship. The primary endpoint is a continuous score, and the registry does not report an over-dispersion analysis; it is not possible to say that over-dispersion occurred or affected this result.

What does the discrepancy mean for inference?

The registry reports two different inferential results: the sponsor’s ANCOVA estimate is -0.2 with p = 0.05, while the simple unadjusted recalculation gives p = 0.882 and a confidence interval from -2.833 to 2.433. These results arise from differently described analyses and cannot be reconciled from the record. Since the discrepancy flag is true, the sponsor’s own analysis takes precedence in reporting the trial result. The recalculation remains useful as a check based on posted summaries, but it should not replace or be presented as the sponsor’s analysis.

There are 2 posted outcome measures and 2 posted analyses, but no secondary results are posted. The registry does not describe a multiplicity adjustment, an analysis hierarchy beyond the primary outcome designation, or a prespecified approach for handling multiple comparisons. General statistical reasoning treats multiple testing as relevant when several hypotheses are evaluated, because repeated testing can increase the chance of at least one apparently notable result. Whether and how that issue was addressed in this study is not reported in the registry record.

10. Confidence Intervals and Precision

The unadjusted recalculation reports a mean difference of -0.2 and a confidence interval from -2.833 to 2.433. This interval includes zero and extends in both directions from the estimated contrast. In general, a confidence interval represents uncertainty around an estimate under the method and assumptions used; it does not guarantee that the true value lies in the interval. The interval’s breadth indicates that the posted summary statistics do not pin down the unadjusted difference narrowly.

The standard errors for the two sequence summaries are each 0.95. These quantify uncertainty in the reported mean estimates, not the range of scores among participants. The registry gives no confidence interval for the sponsor’s ANCOVA estimate. As a result, the sponsor-reported p = 0.05 cannot be paired with a registry-reported interval to assess the precision of that model-based estimate. A p-value by itself does not communicate the range of effect sizes compatible with the analysis.

Interpretation is further limited by the distinction between the sequence summaries and a treatment contrast in a crossover design. The record does not give period-specific estimates, within-participant covariance information, or the sponsor model specification. Without these details, the unadjusted interval should not be treated as an interval from the sponsor’s ANCOVA or as a complete account of crossover uncertainty. The discrepancy between the two analyses reinforces the need to keep their estimates and uncertainty statements separate.

Overall, the recalculated interval permits a range of possible differences, while the sponsor’s reported result lacks a posted confidence interval. The registry record therefore offers limited information for judging the precision of the sponsor’s estimate.

11. 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. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the effect to detect is set to the stated fraction of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

The figures are participants per arm, not total participants and not total events. The outcome is continuous, so the applicable figures are participants per arm. The total-event convention applies to time-to-event illustrations, not to this endpoint. The 80% power column describes the number of participants per arm the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under its assumptions if that effect were real. The 90% power column makes the corresponding planning estimate for a 90% chance.

For planning at 100% of the observed effect, the illustration gives 22,314 participants per arm for 80% power and 29,872 participants per arm for 90% power. Planning for 75% of the observed effect gives 39,669 participants per arm for 80% power and 53,105 participants per arm for 90% power. Planning for 50% of the observed effect gives 89,254 participants per arm for 80% power and 119,486 participants per arm for 90% power. The smaller the effect targeted for detection, the more participants the calculation requires.

These are planning illustrations, not observed power. They depend on the observed effect and stated calculation assumptions, and they are not a retrospective measure of the probability that the trial detected a true effect. Their size should not be taken as a recommendation or as evidence about the trial’s original planning.

12. 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 = -0.200; pooled standard deviation σ = 7.540.
2. n = 2 × (1.96 + 0.842)² × 7.540² / -0.200² = 22,313.4, rounded up to 22,314 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 <- -0.2                      # observed difference in means
sigma <- 7.54039123653408                     # 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(788073)
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 = 22,314 (80% power), 29,872 (90% power)
 75% of observed effect: n per arm = 39,669 (80% power), 53,105 (90% power)
 50% of observed effect: n per arm = 89,254 (80% power), 119,486 (90% power)
power.t.test: 22314.3 
Simulated power at n = 22,314 per arm: 0.802 (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.

13. Analyses Reported by the Sponsor

The registry’s sponsor-reported analysis is an ANCOVA of mean difference in final values. It gives an estimate of -0.2 and p = 0.05. A confidence interval for that estimate is not reported in the registry record. The covariates and full model specification are also not reported, so the analysis cannot be independently reproduced from the registry information.

The unadjusted recalculation based on the posted summary statistics also gives a mean difference of -0.2, but reports a confidence interval from -2.833 to 2.433 and p = 0.882. The estimate is the same as the sponsor-reported value, but the inferential results differ. These are not interchangeable outputs: one is labeled as the sponsor’s ANCOVA, while the other is an unadjusted recalculation from summaries.

Because the discrepancy flag is true, the sponsor’s own analysis takes precedence when describing the trial’s reported result. The recalculation can still provide a transparent check on the posted summary values, but it should not be used to overwrite the sponsor’s analysis or presented as a reproduction of it. The available record does not explain the source of the difference in p-values.

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies the Aberrant Behavior Checklist Irritability Subscore as the primary outcome. It lists 2 outcome measures and 2 analyses, but no secondary results are posted. The record does not state whether a multiplicity adjustment was used, how hypotheses were ordered, or whether any additional outcomes or comparisons were included in a prespecified testing plan. These details are not reported in the registry record.

As a general statistical principle, evaluating multiple outcomes or comparisons can increase the chance of at least one result appearing notable by chance. Methods for addressing multiplicity can include adjusting significance thresholds or defining a hierarchy of tests. The registry information does not establish whether such methods were needed or used in this trial. Therefore, the sponsor-reported p = 0.05 should be interpreted in the context of the primary outcome designation, without assuming that it was or was not adjusted for other analyses.

The record does not report how missing endpoint data were handled, whether participants who did not complete both periods were included, or what analysis population was used. It does not provide participant flow, the number of observations contributing to each estimate, or sensitivity analyses for missing data. Those omissions matter because missing measurements and exclusions can affect both the estimate and its uncertainty, particularly in a crossover design where results from more than one period may contribute.

Other details that would help evaluate the statistical plan, including the original sample-size assumptions, interim analysis plans, and the sponsor model’s covariates, are not reported in the registry record. Their absence does not establish that these procedures were not specified elsewhere; it means the registry record does not document them.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: increased irritability (1.6%).

The registry lists serious adverse events for 1 of 63 participants in the STX209 group and 0 of 63 in the placebo group. The top serious adverse event term is increased irritability, reported as 1.6%. Death counts are not reported in the registry record.

These figures are descriptive counts within the registry’s safety groups. They do not by themselves establish whether an event was caused by treatment, and the record does not provide enough detail to assess attribution, timing, or individual clinical circumstances. The registry also lists other adverse events affecting 42 of 63 participants in the STX209 group and 31 of 63 in the placebo group. These are separate from the serious adverse event counts and should not be combined with them.

For a crossover study, the way safety events are assigned to treatment periods and groups can affect interpretation. The registry does not describe that assignment process or provide period-specific safety results. The listed counts should therefore be read as the posted registry summaries, not as a complete analysis of comparative safety.

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

The posted results describe a small estimated contrast between the two treatment sequences on the primary irritability score: the mean difference is -0.2. The unadjusted recalculation has a confidence interval from -2.833 to 2.433 and p = 0.882. That interval includes zero and covers possible differences in either direction, so the recalculation does not identify a precise nonzero contrast. The sequence summaries themselves are -5.1 and -5.3, with standard errors of 0.95.

The registry also reports the sponsor’s ANCOVA estimate of -0.2 with p = 0.05. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence over the recalculation as the trial’s reported analysis. The record does not provide the sponsor confidence interval, covariates, or sufficient model details to explain why the p-value differs from the unadjusted recalculation. The sponsor result should be reported as such, without treating the unadjusted p-value as its substitute.

These figures do not establish that STX209 works or does not work. They describe the registry’s reported endpoint comparison and the uncertainty information available for that comparison. The outcome is a caregiver-completed irritability subscore, and the primary endpoint is only one part of a broader assessment of efficacy, safety, and tolerability. No secondary results are posted in the registry record.

The crossover design calls for attention to treatment order, periods, and the analysis of repeated observations. The registry does not report those details, missing-data methods, or the analysis population. The safety summary records serious adverse events in the two labeled groups but does not resolve attribution or provide a full period-specific account. These gaps limit how far the posted result can be interpreted beyond its reported statistical summaries.

17. Why This Trial Matters Statistically

This trial illustrates why the design and analysis description matter alongside an estimated effect. In a crossover study, the sequence labels encode treatment order, and interpreting a comparison requires understanding how observations from the different periods were combined. The registry supplies sequence-level summaries and a sponsor analysis label, but does not report period-specific estimates or the full model specification. Those omissions make it important not to treat the design as a simple parallel comparison.

It also illustrates the distinction between a sponsor-reported analysis and a recalculation from summary statistics. Both give a mean difference of -0.2, yet the sponsor’s ANCOVA reports p = 0.05 while the unadjusted recalculation reports p = 0.882 and a confidence interval from -2.833 to 2.433. A shared point estimate does not guarantee the same uncertainty estimate or inferential conclusion. Keeping the analyses distinct is essential to an accurate reading of the record.

Finally, precision and planning are related but separate questions. The confidence interval from the recalculation spans a range of possible contrasts, while the sample-size figures are planning illustrations based on the observed effect and explicit assumptions. They do not describe observed power or the study’s original design. Together, these features show why effect estimates, uncertainty, model details, and planning assumptions should be read as different components of statistical evidence.

18. Limitations

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

The registry record leaves several trial-specific questions unresolved. Although it describes a crossover study and lists the two treatment sequences, it does not report period-specific results, the interval between periods, or whether carryover or sequence effects were assessed. It also does not provide the sponsor ANCOVA covariates or full model specification. These omissions prevent a detailed reconstruction of the primary analysis.

The record lists enrollment and sequence-level n values, but does not report participant flow, the analysis population, or how many observations contributed to each endpoint estimate. Missing-data handling and sensitivity analyses are not reported in the registry record. This makes it difficult to judge how incomplete participation or measurements may have affected the comparison.

The sponsor’s reported p-value differs from the unadjusted recalculation, and the registry provides no sponsor confidence interval to clarify precision. The discrepancy is not explained in the record. The unadjusted recalculation uses an approximate pooled standard deviation, so it is not equivalent to the sponsor’s model-based result.

Safety information is also limited to posted group counts and a top serious adverse event term. The record does not report deaths, event attribution, or period-specific safety summaries. Finally, the original sample-size justification, interim analyses, multiplicity approach, and statistical plan are not reported in the registry record. These are limitations of what the registry documents, rather than evidence that the procedures were not addressed elsewhere.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Safety, Tolerability and Efficacy Study of STX209 in Subjects With Fragile X Syndrome — NCT00788073.
• Registry record last updated 2013-05-06; status last verified 2013-03.
• Results first posted 2013-05-06.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT00788073 is a completed Phase 2 randomized, quadruple-masked, placebo-controlled crossover study of STX209 in subjects with Fragile X Syndrome. The registry lists enrollment of 63 and two treatment sequences, STX209:Placebo and Placebo:STX209. Each intervention period is described as 4 weeks.

The primary endpoint was the Aberrant Behavior Checklist Irritability Subscore after 4 weeks of treatment. The sponsor-reported ANCOVA estimate is -0.2 with p = 0.05. An unadjusted recalculation gives the same mean difference, a confidence interval from -2.833 to 2.433, and p = 0.882. The registry flags a discrepancy; the sponsor’s own analysis takes precedence, while its confidence interval and full model details are not reported in the registry record.

Safety summaries list 1 serious adverse event in the STX209 group and 0 in the placebo group. The registry does not post secondary results or report several analysis details needed for fuller interpretation.