Combining Lovastatin and a Parent-Implemented Language Intervention for Fragile X Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Combining Lovastatin and a Parent-Implemented Language Intervention for Fragile X Syndrome (NCT02642653), a randomized phase 4 study. The primary outcome is Expressive Language Sample Composite Score in the Home.

2. Clinical Question

3. Trial Design

The registry identifies NCT02642653 as a completed Phase 4 randomized parallel-group trial sponsored by the University of California, Davis. Enrollment is recorded as 30. The study start is listed as 2016-01 and primary completion as 2018-07. The record describes quadruple masking, but does not specify the identities of all masked roles in the information.

Participants were assigned to one of two arms: lovastatin with PILI, or placebo with PILI. The study summary describes a 20 week treatment period and says that participating children were randomized to drug or placebo in a double-blind design, with all taking part in PILI. The intervention descriptions likewise pair the medication or placebo with PILI. These details establish the intended contrast as medication versus placebo against a shared language-intervention background; they do not establish how consistently the intervention was delivered or followed.

The primary outcome is a continuous score, summarized by means and standard deviations. The registry’s primary outcome timeframe is Baseline. The posted arm summaries list 12 participants for lovastatin and PILI and 16 for placebo and PILI. These counts are the reported sample sizes for the displayed primary measure; the record does not provide a participant-flow account explaining the relation between those counts and the enrollment of 30.

Although the registry lists secondary outcomes, it reports no analyses in the analysis fields. The record also does not report the original statistical analysis plan, the trial’s sample-size justification, or the details of allocation concealment. Those design features cannot be inferred from the randomized and masking labels alone.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

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 Expressive Language Sample Composite Score in the Home, measured over Baseline.

The primary endpoint is the Expressive Language Sample Composite Score in the Home. The registry describes it as reflecting the diversity of vocabulary used. Higher scores indicate more skill. Its lowest possible value is zero, while no theoretical maximum can be defined: wordless picture books may prompt an indeterminate amount of talk and vocabulary. The score is therefore not bounded above by a stated scale maximum.

A home language sample can capture vocabulary use in a setting intended to elicit spoken language, making it relevant to the trial’s language objective. The registry describes this measure as a score on a scale and summarizes it as a mean with a standard deviation. Those summaries describe the distribution of scores in each arm; they do not, by themselves, show improvement over time or attribute a difference to treatment.

The key interpretive qualification is the recorded timeframe: Baseline. The posted primary values are 39.63 for lovastatin and PILI and 42.47 for placebo and PILI. They describe the arms at baseline, before the treatment period described in the study summary. The registry record does not report a post-treatment primary score or a change-from-baseline estimate. A baseline comparison can describe how the randomized groups started, but it cannot answer whether their language outcomes changed differently after treatment.

7. Results Posted in the Registry

• Lovastatin and PILI: mean 39.63 versus 42.47 on control; difference -2.84 (95% CI -23.32 to 17.64), standardized effect d = -0.11; z-test p = 0.786.

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.

FXS- Normed Aberrant Behavior Checklist (ABC) Social Avoidance Subscale

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Lovastatin and PILI: mean 2.50 versus 4.31 on control; difference -1.81 (95% CI -4.22 to 0.60), standardized effect d = -0.54; z-test p = 0.141.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lovastatin and PILI and the control. The interval gives the range of effects that remain compatible with the data.

Clinical Global Impression- Severity (CGI-S)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Lovastatin and PILI: mean 4.58 versus 4.50 on control; difference 0.08 (95% CI -0.41 to 0.57), standardized effect d = 0.12; z-test p = 0.748.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lovastatin and PILI and the control. The interval gives the range of effects that remain compatible with the data.

Clinical Global Impression-Improvement (CGI-I) Scale

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Lovastatin and PILI: mean 2.92 versus 3.00 on control; difference -0.08 (95% CI -0.65 to 0.49), standardized effect d = -0.11; z-test p = 0.784.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Lovastatin and PILI and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover behavioral and clinical ratings as well as a spoken-language impairment rating. The posted summaries include baseline measures and a Clinical Global Impression-Improvement measure with a 10 weeks timeframe. That mix of domains and timings means the secondary outcomes should not be treated as interchangeable measures of a single underlying result.

Across the posted secondary comparisons, the estimates do not form a consistent, clearly established pattern that can resolve the primary question. Their uncertainty intervals include zero, and the comparisons are unadjusted. The registry record reports no analyses in its analysis fields. These features make the secondary findings exploratory descriptions of the posted summaries rather than confirmatory evidence about the treatment objective.

The secondary outcomes can provide context for the primary language measure because the study objective includes behavior as well as spoken language. However, a baseline secondary comparison cannot demonstrate change after treatment. A follow-up rating can address a different time point, but without a reported analysis plan, complete endpoint results, or multiplicity handling, it cannot by itself establish that the intervention altered a behavioral or clinical outcome. Nor can the secondary summaries supply the missing post-treatment primary language result.

Multiple outcomes create multiple opportunities to observe an apparently notable result by chance. Unadjusted secondary comparisons do not account for that multiplicity, so their p-values and intervals should carry less weight than results from a prespecified, appropriately analyzed primary endpoint. The registry record does not state a hierarchy among secondary outcomes or a multiplicity strategy. The most defensible reading is therefore to regard the secondary summaries as descriptive and supportive at most, while keeping their limitations distinct from the baseline-only primary result.

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

• FXS- Normed Aberrant Behavior Checklist (ABC) Social Avoidance Subscale
• FXS- Normed Aberrant Behavior Checklist (ABC) Social Avoidance Subscale
• FXS- Normed Aberrant Behavior Checklist (ABC) Social Avoidance Subscale
• Clinical Global Impression- Severity (CGI-S)
• Clinical Global Impression-Improvement (CGI-I) Scale
• Clinical Global Impression-Improvement (CGI-I) Scale
• Visual Analog Scale (VAS) - Spoken Language Impairment
• Visual Analog Scale (VAS) - Spoken Language Impairment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, so the registry reports a mean and standard deviation in each arm. A mean gives the arithmetic average of the observed scores. A standard deviation describes how spread out individual scores are around that average. These summaries are useful for describing the groups, but they do not show the full distribution of scores or how each participant’s score changed over time.

The posted comparison is a mean difference: the lovastatin and PILI mean minus the placebo and PILI mean. For the primary baseline measure, the estimate is -2.84. A negative sign means that the reported mean was lower in the lovastatin and PILI arm at baseline. Because higher values reflect more skill, that direction describes the starting scores only. It does not describe a treatment-related decrease or improvement.

A confidence interval expresses uncertainty around an estimate under the statistical method used. The 95% interval for the primary mean difference is -23.32 to 17.64. Its span indicates that the estimate is imprecise; it includes zero and values on either side. A confidence interval is not a range containing a fixed proportion of individual participants’ scores, and it does not correct for limitations in outcome timing, missing data, or analysis choices. The registry does not report a sponsor analysis for this result; the displayed estimate and interval are unadjusted recalculations from the posted summary statistics.

The unadjusted p-value for the primary contrast is 0.786. A p-value describes how unusual the observed result, or a more extreme result, would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. Here, it concerns the baseline contrast and should not be read as a test of treatment efficacy. No adjustment for multiple comparisons is reflected in this unadjusted value.

Standard deviation and standard error serve different purposes. A standard deviation describes variability among individual scores, whereas a standard error characterizes the uncertainty of an estimate such as a group mean. The posted primary standard deviations are 32.41 and 18.6; the arm standard errors listed in the calculation are 9.356 and 4.65. The uncertainty in a mean depends partly on the number of observations and the variability among them. The reported counts are 12 and 16, respectively.

A pooled standard deviation is used in some standardized comparisons to express a mean difference relative to a common measure of variability. The primary pooled standard deviation listed for the recalculation is 25.38, and the corresponding standardized difference is -0.112. Standardization can help compare measures expressed on different scales, but it does not resolve whether the endpoint was measured after treatment. The standardized value remains a description of the baseline contrast.

Randomization is intended to make the assigned groups comparable on average, while masking is intended to reduce the influence of expectations on trial conduct or assessment. Those design labels do not guarantee that every observed baseline feature will be identical, particularly in a trial with a limited enrollment. Nor do they replace outcome analysis. A treatment comparison ordinarily needs outcome measurements at an appropriate follow-up time, and the analysis should account for the design and any missing observations. The registry record does not report such a primary follow-up analysis.

Over-dispersion is a general concern when observed outcomes vary more than a model assumes. In that situation, standard errors can be understated and confidence intervals too narrow if the model does not account for the extra variability. The primary outcome has a broad observed spread, but the posted summaries do not provide enough information to diagnose a distributional model or assess outliers. It would be inappropriate to infer the presence or absence of over-dispersion from the means and standard deviations alone.

Likewise, the normal approximation used in the planning illustration is an assumption for that illustration, not evidence that the endpoint data follow a normal distribution. General statistical practice treats model assumptions as questions to check against data and design details. The record does not report diagnostic checks, transformations, covariate adjustment, or a model for repeated measures.

The distinctions among a baseline comparison, a follow-up comparison, and a change comparison are important. A baseline comparison contrasts the groups before treatment. A follow-up comparison contrasts their scores at a later time. A change comparison considers how scores moved from baseline within each group and contrasts those changes. They answer different questions and may have different uncertainty. Only the first type is available for the posted primary measure, because its registered timeframe is Baseline and no post-treatment primary result is reported.

Finally, statistical evidence and clinical meaning are not interchangeable. Statistical summaries quantify patterns and uncertainty under chosen methods; they do not establish that a measured difference matters to children or families. The registry does not report a threshold for a meaningful score change. Without that information and a post-treatment primary analysis, the baseline estimate cannot establish the practical importance of a treatment-related effect.

11. Confidence Intervals and Precision

The primary baseline mean difference is -2.84, with a 95% confidence interval from -23.32 to 17.64. The interval extends from a negative contrast to a positive contrast and includes zero. It therefore does not pin down the direction of a baseline difference with precision. Its width also means that the point estimate should not be treated as an exact description of the underlying contrast.

Confidence intervals quantify sampling uncertainty under the calculation’s assumptions. They do not include every possible source of uncertainty, such as unreported outcome procedures, missing observations, or choices made in an analysis plan. The registry record does not report a sponsor analysis, a primary follow-up estimate, or details of any adjustment for baseline characteristics. The interval is consequently best understood as an unadjusted summary-statistic recalculation for the baseline data.

Precision is distinct from whether a result is statistically significant and from whether a result is important to participants. A narrow interval can provide a more precise estimate without establishing clinical importance; a wide interval can leave substantial uncertainty even when the point estimate looks small. Here, the interval’s inclusion of values in both directions reinforces that the baseline data do not establish a clear directional contrast. More importantly, no interval is reported for the primary treatment-related change because the registry record does not report a post-treatment primary analysis.

The different arm standard deviations, 32.41 and 18.6, also indicate differing observed spread in the baseline summaries. The registry record does not provide participant-level data or distributional diagnostics with which to investigate that difference. Precision should therefore be read alongside the endpoint timing and the limited information about analysis methods, not as a stand-alone judgment about the study’s treatment question.

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 in the posted summary statistics, not the trial’s original design assumptions. The stated illustration assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers an effect equal to the stated fraction of the observed effect. For these continuous outcomes, the figures are participants per arm, not a combined total and not a count of events.

The 80% power column gives the illustrative number of participants per arm for an assumed design to have an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are theoretical design calculations, not guarantees about what a future trial would detect. They depend on the assumed effect and the planning model.

Rows planning for 75% or 50% of the observed effect represent smaller effects than the row using 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same assumptions. This pattern is a general feature of power planning, not evidence that an effect of any particular size is real or meaningful.

The calculations use the observed effect for the corresponding posted comparison. Because the primary comparison is a baseline contrast, its planning illustration is based on that baseline estimate; it is not a sample-size justification for the trial’s intended treatment question. The registry record does not report the trial’s original sample-size justification or original design assumptions. These figures are not observed power.

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 = -2.840; pooled standard deviation σ = 25.377.
2. n = 2 × (1.96 + 0.842)² × 25.377² / -2.840² = 1,253.4, rounded up to 1,254 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 <- -2.84                      # observed difference in means
sigma <- 25.3770710409098                     # 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(2642653)
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 = 1,254 (80% power), 1,678 (90% power)
 75% of observed effect: n per arm = 2,229 (80% power), 2,983 (90% power)
 50% of observed effect: n per arm = 5,014 (80% power), 6,712 (90% power)
power.t.test: 1254.3 
Simulated power at n = 1,254 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. Multiplicity, Missing Data and Analysis Populations

The registry record lists several secondary outcome measures, including repeated entries for the ABC Social Avoidance Subscale, Clinical Global Impression measures, and a Visual Analog Scale for spoken language impairment. It also records 14 outcome measures and zero analyses in the analysis fields. The repeated measure names and the number of listed measures indicate that more than one outcome was under consideration, but the record does not report how the investigators planned to control the risk of false-positive findings across outcomes or time points.

No multiplicity adjustment or prespecified testing hierarchy is reported in the registry record. The unadjusted secondary comparisons should therefore not be interpreted as if they were protected by a familywise error procedure or another correction. The record also does not report which secondary outcomes were designated confirmatory, how outcomes at different times were to be prioritized, or whether any interim analyses were planned. Those details are not reported in the registry record.

Missing-data handling is also not reported in the registry record. There is no description of imputation, mixed models, sensitivity analyses, or rules for excluding observations. The posted arm counts differ by measure and timing in the summaries available, but the record does not provide participant flow or reasons for unavailability. It is not possible to determine from these summaries whether missing observations were related to treatment, outcome, or other factors.

The analysis populations are not reported in the registry record. It does not specify whether an intention-to-treat, per-protocol, or other population was used for any primary treatment analysis. The posted summaries alone cannot establish whether all randomized participants were included or how deviations from assignment were handled. These omissions matter because analysis population and missing-data choices can affect estimated effects and their uncertainty.

Finally, the registry does not report a formal analysis of the primary treatment objective. Its primary endpoint timeframe is Baseline, and no post-treatment primary contrast or change analysis appears in the posted record. Consequently, multiplicity, missing-data, and analysis-population considerations cannot be evaluated against a reported primary efficacy analysis.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events in the lovastatin and PILI arm among 12 participants at risk, and zero in the placebo and PILI arm among 16 participants at risk. It also reports zero deaths in both arms. These are the counts recorded for the groups and should be read as event summaries, not as proof that serious events could not occur.

For other adverse events, the record lists 11 affected participants among 12 at risk in the lovastatin and PILI arm and 13 among 16 at risk in the placebo and PILI arm. The registry’s serious-event term list is empty. It does not provide event descriptions in the information, so the types, timing, severity beyond the serious classification, and relationship to study treatment cannot be characterized from these counts.

Safety counts are descriptive. The registry record does not report a comparative statistical analysis of adverse events, nor does it explain the event-collection period in the entries. Zero reported serious events should not be interpreted as evidence of equal safety between arms or as evidence that no unrecorded or unobserved events occurred.

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

The posted primary result is a comparison of baseline language scores, not a comparison of treatment outcomes. The mean score was 39.63 in the lovastatin and PILI arm and 42.47 in the placebo and PILI arm; the unadjusted difference was -2.84, with a 95% confidence interval from -23.32 to 17.64. These figures describe how the groups were scored at baseline in the posted summaries.

They do not show that lovastatin improved spoken language, that placebo did or did not improve language, or that the two groups changed differently. They also do not establish that the arms were identical at baseline. The interval allows for a range of possible baseline contrasts, and the registered timeframe means the estimate does not address the stated post-treatment objective.

The study summary describes a 20 week multimodal treatment and a primary aim concerning improvements in spoken language and behavior. Yet the primary measure is recorded at Baseline, and the registry record does not report a post-treatment primary value or change analysis. The registry record also reports no analyses in its analysis fields. Accordingly, the result cannot be used to conclude whether adding lovastatin to PILI affected the language outcome.

The secondary summaries do not fill that gap. Some are baseline measures, while one posted Clinical Global Impression-Improvement outcome has a 10 weeks timeframe. They are multiple, unadjusted comparisons, and the record does not report a multiplicity plan or a complete primary analysis framework. They may describe selected outcomes at their recorded timeframes, but they do not establish the primary treatment effect.

Nor do the sample-size illustrations indicate whether the trial had adequate power for its original purpose. They use the observed effects and stated planning assumptions to give hypothetical participant counts; they are not observed power and are not the original sample-size justification. Overall, the registry’s posted figures support a cautious description of baseline groups and recorded adverse-event counts, but leave the main treatment question unanswered in the reported primary outcome results.

17. Why This Trial Matters Statistically

This trial illustrates why outcome timing is essential to interpreting a randomized study. Random allocation, masking, and a clearly described comparator establish important parts of the design, but they do not make a baseline score a treatment result. A result must be tied to the time at which the outcome was measured and to the question the analysis answers.

The contrast is especially relevant when both arms receive an active behavioral intervention. The randomized comparison is lovastatin plus PILI versus placebo plus PILI, not PILI versus no intervention. That design can address the added contribution of the medication only when an appropriately timed comparison of outcomes is reported. The baseline summaries alone cannot do so.

The case also shows why uncertainty deserves attention alongside point estimates and p-values. The primary confidence interval includes contrasts in either direction, while the listed standard deviations differ between arms. Reporting the interval and the underlying arm summaries makes clear that the baseline estimate is not precise enough to support a simple directional reading. Statistical significance alone would not resolve the mismatch between baseline timing and a post-treatment research question.

Finally, a registry record is useful for documenting design features and posted results, but incomplete analysis reporting limits independent interpretation. The absence of a reported primary follow-up analysis, multiplicity strategy, missing-data method, and analysis population leaves key statistical questions unresolved. Clear outcome timing and transparent analysis reporting are necessary for readers to distinguish descriptive baseline information from evidence bearing on a treatment objective.

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 main trial-specific limitation is that the registered timeframe for the primary endpoint is Baseline. The study objective concerns a 20 week multimodal treatment, but the registry record does not report a post-treatment primary result, a change-from-baseline estimate, or an analysis comparing changes between arms. This prevents the posted primary values from answering the treatment question.

The reported primary arm counts are 12 and 16, while overall enrollment is listed as 30. The record does not provide a participant-flow explanation for the difference between enrollment and the counts in these summaries. It also does not state whether the posted summaries represent all randomized participants, which observations were available at each time point, or why observations might be absent.

The primary measure has no theoretical maximum and shows different standard deviations between arms in the posted baseline summaries. Without participant-level data or distributional diagnostics, it is not possible to assess score distributions, unusual observations, or the robustness of a mean-based comparison. The registry does not report whether any covariate adjustment or alternative model was planned.

Additional limitations are the absence of reported analyses in the analysis fields and the lack of a reported multiplicity strategy, missing-data method, or analysis population. The record also does not report the original sample-size justification. The planning figures calculated from observed effects cannot resolve those omissions or show that the original trial design was adequate for the intended treatment question.

The secondary outcomes span different constructs and timeframes, and their unadjusted comparisons do not constitute a prespecified confirmatory analysis. The safety counts are also descriptive and contain no comparative statistical assessment. These limitations apply to interpretation of the registry record; they do not establish what analyses may or may not exist outside that record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Combining Lovastatin and a Parent-Implemented Language Intervention for Fragile X Syndrome — NCT02642653.
• Registry record last updated 2019-09-11; status last verified 2019-08.
• Results first posted 2019-09-11.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT02642653 is a completed randomized, quadruple-masked, parallel-group Phase 4 trial sponsored by the University of California, Davis, with enrollment recorded as 30. Children with Fragile X syndrome were assigned to lovastatin plus PILI or placebo plus PILI. The study summary describes a 20 week multimodal treatment.

The primary endpoint is the Expressive Language Sample Composite Score in the Home, a vocabulary-diversity measure for which higher scores reflect more skill. Its registered timeframe is Baseline. The posted baseline means are 39.63 for lovastatin and PILI and 42.47 for placebo and PILI; the unadjusted mean difference is -2.84, with a 95% confidence interval from -23.32 to 17.64 and p = 0.786.

The registry record reports no analyses in its analysis fields and does not report a post-treatment primary analysis. The posted primary values therefore describe baseline scores, not treatment-related change.