Evaluation of the Efficacy, Safety, and Tolerability of Sarizotan in Rett Syndrome With Respiratory Symptoms: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of the Efficacy, Safety, and Tolerability of Sarizotan in Rett Syndrome With Respiratory Symptoms (NCT02790034), a randomized phase 2, phase 3 study. The primary outcome is Reduction in Respiratory Abnormality in Patients With Rett Syndrome.

2. Clinical Question

3. Trial Design

The registry identifies this as a randomized, parallel-group study with quadruple masking and phase 2 and phase 3 designations. It lists 129 participants enrolled. The study title describes a 6-month trial, while the brief summary specifies an initial double-blind period of 24 weeks followed by an open-label phase of up to 168 weeks for patients without safety or tolerability issues. The primary endpoint timeframe ends at week 24, so the posted primary results concern the initial blinded period rather than the longer open-label phase.

Participants were assigned to sarizotan low dose, sarizotan high dose, or placebo. The active-dose descriptions indicate that the twice-daily dose depended on age and weight. Placebo was given twice daily during the blinded period. The registry does not report how many participants entered or completed the open-label phase in the record details available for this analysis.

The registry lists Newron Pharmaceuticals SPA as sponsor, gives the study start as 2016-10-26, and gives primary completion as 2019-08-06. Its status is terminated. The registry record does not explain the reason for termination, and termination alone does not establish why the study stopped or what would have happened with continued follow-up. The record does not report the original design assumptions used to select the enrollment target, nor does it report interim analyses or detailed allocation procedures.

For the primary efficacy outcome, the stated analysis population was the intention-to-treat population, defined as all patients randomized to treatment. The registry says this population was used for all efficacy analyses. The sponsor's posted primary analyses are described as mixed models comparing final values. More detail about model specification, covariate adjustment, and handling of missing observations is 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.

Before assignment: A total of 198 patients were screened, of which 69 (34.8%) patients were screen failures. A total of 129 patients were randomized in the study. A total of 128 patients were exposed to at least one dose of IMP, with placebo ITT group (40) vs safety pop (39).

Overall Study

Analysis population for the primary outcome, as defined in the registry: The ITT population included all patients who were randomized to treatment. This population was used for all efficacy analysis.

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 Reduction in Respiratory Abnormality in Patients With Rett Syndrome, measured over Baseline up to week 24.

The primary endpoint is the percent change from baseline through week 24 in the mean number of apnea episodes per hour during awake time. Respiratory episodes were measured with an ambulatory data acquisition system, BioRadio, as part of home monitoring. The registry says the system recorded respiratory and cardiac parameters. The reported unit is percent change in mean counts per hour, and the summary statistic is a least-squares mean with standard error.

Apnea episodes during awake time provide a count-based measure of one respiratory abnormality relevant to the study population. Expressing the outcome as a change from baseline is intended to describe how the measured rate changed during treatment, rather than only the endpoint value. A comparison with placebo helps distinguish changes observed during active treatment from changes that may also occur over time in the comparison group. These are general reasons for using a baseline-change outcome and a concurrent control; they do not establish that the measure captures every clinically important aspect of Rett syndrome or respiratory health.

The endpoint relies on home monitoring, so its meaning depends on the consistency and completeness of the recordings and on how recorded episodes were converted into counts per hour. The registry describes the monitoring system but does not report detailed rules for invalid recordings, missing monitoring periods, or endpoint adjudication. It also does not report a minimally important difference for the measure. Accordingly, the numerical changes describe the posted outcome on its stated scale, but their clinical importance cannot be determined from the registry record alone.

7. Results Posted in the Registry

• Sarizotan Low Dose: mean 1.54 versus 18.50 on control; difference -16.96 (95% CI -42.80 to 8.87), standardized effect d = -0.31; z-test p = 0.198.
• Sarizotan High Dose: mean 13.21 versus 18.50 on control; difference -5.29 (95% CI -27.43 to 16.85), standardized effect d = -0.10; z-test p = 0.639.

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.

Efficacy of Sarizotan Assessed by the Caregiver-rated Impression of Change

• 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:
  • Sarizotan Low Dose: mean 3.60 versus 3.40 on control; difference 0.20 (95% CI -0.13 to 0.53), standardized effect d = 0.27; z-test p = 0.242.
  • Sarizotan High Dose: mean 3.50 versus 3.40 on control; difference 0.10 (95% CI -0.28 to 0.48), standardized effect d = 0.10; z-test p = 0.608.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sarizotan Low Dose and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sarizotan High Dose and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary outcome: caregiver-rated Impression of Change at 24 weeks. It is a score on a scale, summarized as a mean with standard deviation. The posted arm summaries place the group means close together, and the unadjusted comparisons have intervals that include zero. Taken across the posted secondary evidence, there is no clear separation from placebo in this measure. Because only one secondary outcome is listed in the posted results, the record does not support a broader pattern across several distinct secondary measures.

This secondary outcome complements, rather than duplicates, the primary respiratory measure. The primary endpoint is based on monitored apnea episodes per hour during awake time; the secondary outcome reflects a caregiver rating. Agreement between different kinds of outcomes can be informative, but they measure different aspects of experience and are not interchangeable. The secondary result does not resolve the uncertainty in the primary comparison, and the primary result does not establish what caregivers would rate on a broader or different outcome.

The registry record does not report a multiplicity adjustment for testing secondary outcomes. General explanation: when several hypotheses are tested, the chance of at least one apparently notable result can increase if each test is judged independently. Unadjusted secondary results therefore generally carry less confirmatory weight than a prespecified primary analysis, particularly when the number of planned comparisons and the adjustment strategy are not clear. The record's limited secondary reporting also does not establish whether other outcomes were measured but not posted. The secondary finding is best regarded as supportive descriptive context, not as independent confirmation of a treatment effect.

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

• Efficacy of Sarizotan Assessed by the Caregiver-rated Impression of Change

9. Statistical Interpretation

10. Statistical Methods Explained

The sponsor's reported primary analysis is a mixed-model analysis of final values, with the parameter described as mean difference. The posted least-squares means summarize the outcome in each treatment group after model-based estimation. In general, a least-squares mean is a model-derived group mean; depending on the model, it may account for specified covariates or other structure. The registry record does not report the model formula, included covariates, covariance structure, or other implementation details, so the exact role of those elements cannot be assessed from the record.

The posted recalculations use the arm-level summaries to form simple unadjusted comparisons with placebo. For the primary endpoint, the estimate is the active-group mean minus the placebo mean. The recalculations are not the sponsor's mixed-model analyses. They use the reported means and standard errors to obtain an approximate pooled spread and an unadjusted interval and p value. In the primary comparisons, the posted standard errors were used to approximate standard deviations. That conversion is marked as approximate in the calculation details, so the recalculated uncertainty should be understood as an approximation based on summary statistics, not a reproduction of participant-level modeling.

General explanation: an unadjusted comparison uses the group summaries without incorporating covariate adjustment or other model features. A mixed model can use a specified structure for the observed data and may account for factors included in its formula. Neither method is automatically preferable in every setting; their suitability depends on the design, data, and prespecified analysis plan. The registry does not provide enough detail to evaluate the sponsor model's specification or compare its assumptions fully with those of the simple recalculation.

A standard error describes the estimated sampling variability of a group summary or contrast. It is not the spread of individual participant outcomes. A standard deviation describes variation among observations, while a standard error generally becomes smaller as the information contributing to an estimate increases. In this record, the primary arm summaries are reported as least-squares means with standard errors, not as means with standard deviations. The distinction is important when comparing the reported dispersion with the recalculated pooled spread.

General explanation: the p value measures how unusual the observed result, or a more extreme one, would be under a specified null hypothesis and the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. A confidence interval gives a range of estimates compatible with the data and analysis procedure. When an interval for a mean difference includes zero, it includes no difference as one value consistent with the data; that does not prove that the true difference is zero.

The outcome is expressed as a percent change in a rate of apnea episodes. Counts and rates can show substantial variability, and their statistical behavior may depart from assumptions of simple normal models. General explanation: over-dispersion occurs when variation in count data exceeds what a chosen probability model expects. If present, it can make standard errors too small unless the analysis allows for the extra variation. The registry entries do not report a diagnostic assessment of over-dispersion or a count-data model, and the posted primary summary is a least-squares mean on a percent-change scale. It is therefore not possible to determine from the record whether over-dispersion was evaluated or how it would affect the sponsor's analysis.

Randomization aims to make treatment groups comparable on average with respect to measured and unmeasured baseline factors, but it does not guarantee balance in every realized trial. Masking can reduce some forms of bias in treatment delivery, assessment, and interpretation. The registry classifies this study as quadruple masked but does not identify in the record details which roles were masked or how masking was maintained. These design features provide context for the comparison; they do not remove uncertainty caused by outcome variability, missing data, or limited precision.

The sponsor's mixed-model estimates are the appropriate results to cite as the trial's own reported primary analysis. The unadjusted recalculations are useful as a transparent secondary check based on the posted arm summaries. The estimates are close in broad magnitude, and both approaches yield intervals that include zero and p values above 0.05. The recalculations should not be treated as a substitute for the sponsor's analysis, especially because the participant-level data and full statistical plan are not available in the registry record.

The stated efficacy population is intention-to-treat and includes all randomized patients. General explanation: an intention-to-treat approach retains participants in their randomized groups for analysis, which helps preserve the comparison created by randomization. That label does not by itself reveal how missing endpoint observations were handled. The specific imputation method, assumptions about missingness, sensitivity analyses, and numbers with observed endpoint data are not reported in the registry record. Those omissions limit assessment of how robust the endpoint estimates are to incomplete monitoring or follow-up.

11. Confidence Intervals and Precision

The sponsor reports 95% confidence intervals for both primary comparisons. For sarizotan low dose versus placebo, the sponsor's estimate is -16.966, with a 95% confidence interval from -43.119 to 9.186. For sarizotan high dose versus placebo, the estimate is -5.292, with a 95% confidence interval from -27.741 to 17.157. Both intervals extend across zero. They therefore include no difference as well as values on either side of zero, and neither comparison is estimated with enough precision to exclude a null contrast using these intervals.

The unadjusted recalculated intervals are also broad: -42.8 to 8.87 for low dose and -27.43 to 16.85 for high dose. These intervals are derived from posted summary statistics and are not the sponsor's mixed-model intervals. Their general overlap with the sponsor intervals supports a similar reading of uncertainty, while the differences in endpoints show that the methods are not identical. The sponsor's own model results remain the trial's reported analysis.

General explanation: interval width reflects the precision of an estimate under the analysis assumptions. A narrower interval indicates greater precision; a wider interval leaves a broader range of plausible values. Precision is distinct from whether a test crosses a significance threshold. In this study, the intervals are wide enough to allow effects that could be meaningfully different from the point estimates, including no difference. The registry does not report a clinical threshold for an important difference, so the intervals cannot be classified against such a threshold.

The arm-level standard errors are 10.12 for low dose, 7.508 for high dose, and 8.441 for placebo. These values describe uncertainty around the reported least-squares means, not the variability of individual outcomes. The modest sizes of the treatment groups and the variability reflected by these standard errors contribute to limited precision, though the registry record does not provide a formal decomposition of sources of uncertainty. Precision also depends on the analysis model, endpoint completeness, and data quality, details that are not fully reported.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for the two-arm comparison, not total participants across the trial. Each active dose is considered separately against placebo. The calculations use the observed effect as a reference and show planning for 100%, 75%, and 50% of that observed effect. For example, the low-dose comparison lists 169 participants per arm for 80% power when planning for 100% of the observed effect; for 75% of the observed effect it lists 300 participants per arm, and for 50% it lists 675 participants per arm. The high-dose comparison lists 1,698 participants per arm for 80% power at 100% of the observed effect; its corresponding figures for 75% and 50% are 3,019 and 6,792 participants per arm.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The stated effect to detect is the selected fraction of the observed effect. The 90% power column gives the participants per arm required for a higher chance of detecting an effect of that assumed size, if the effect and planning assumptions hold. The 80% power column represents a lower target chance of detection under those same conditions. A smaller assumed effect requires more participants to reach either target, as reflected in the increasing figures across the planning rows.

These are illustrations based on the observed effects, not the original trial's design calculations. The assumptions used for the trial's original sample-size justification are not reported in the registry record. The figures are not observed power: they do not measure the probability that this completed trial detected an effect, and they should not be used as a retrospective verdict on the trial. The registry does not report a time-to-event planning outcome in these calculations, so the displayed quantities are participants per arm rather than total events.

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 = -16.963; pooled standard deviation σ = 55.584.
2. n = 2 × (1.96 + 0.842)² × 55.584² / -16.963² = 168.6, rounded up to 169 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 <- -16.963                      # observed difference in means
sigma <- 55.583994386752                     # 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(2790034)
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 = 169 (80% power), 226 (90% power)
 75% of observed effect: n per arm = 300 (80% power), 402 (90% power)
 50% of observed effect: n per arm = 675 (80% power), 903 (90% power)
power.t.test: 169.5 
Simulated power at n = 169 per arm: 0.799 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor's own primary comparisons use mixed models and report mean differences in final values. For low dose versus placebo, the sponsor estimate is -16.966, with a 95% confidence interval from -43.119 to 9.186 and p=0.201. For high dose versus placebo, the estimate is -5.292, with a 95% confidence interval from -27.741 to 17.157 and p=0.641. Both sponsor intervals include zero, and both p values are above 0.05.

The unadjusted recalculations from the posted summaries produce estimates of -16.96 for low dose and -5.292 for high dose. Their intervals and p values are close in broad inferential meaning to the sponsor's, although the interval endpoints and p values are not identical. The recalculations use summary statistics and approximations, while the sponsor reports mixed-model results. They therefore serve as a check on the broad pattern, not as a replacement or correction of the trial analysis.

The registry entries do not flag a discrepancy. The sponsor's reported model analysis should be treated as the primary account of the trial's own inferential results; the recalculations offer a simpler, unadjusted perspective. Both leave substantial uncertainty around the treatment contrasts and do not provide clear statistical evidence of a difference from placebo.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary efficacy outcome and one posted secondary outcome, and it reports two primary treatment comparisons against placebo. The record does not report whether the analysis plan adjusted for testing two active doses or for other planned outcomes. It also does not state a hierarchy for the comparisons or define how a family of tests would be interpreted. Without that information, the reported p values should be read as the values for their individual analyses, not as evidence that a trial-wide multiplicity procedure was applied.

General explanation: multiplicity arises when more than one statistical hypothesis is tested. If each test uses the same threshold without adjustment, the overall chance of at least one false-positive result can be higher than the threshold for an individual test. Adjustment methods or a prespecified testing sequence can address that issue, but no such procedure is described in the registry entries. This limitation does not change the fact that the posted primary comparisons are not statistically significant at 0.05; it does affect how strongly individual positive results would ordinarily be interpreted if they had occurred.

The stated efficacy population is intention-to-treat and includes all randomized patients. This is useful information about the analysis population, but the registry does not report the number with observed primary endpoint data in each group or how missing values were treated. The missing-data assumptions, imputation method, and sensitivity analyses are not reported in the registry record. For a home-monitoring endpoint, the completeness and usability of recordings are relevant to interpreting the analysis, but the record does not provide the detail needed to assess them.

The registry describes a mixed-model analysis but does not give its complete specification. It does not report the covariates, missing-data handling within the model, diagnostics, or sensitivity analyses. Interim analyses and stopping rules are also not reported. These absences should be treated as limits on what can be evaluated from the record, rather than evidence that a particular procedure was or was not used. The original sample-size justification and its assumptions are not reported either, so the planning illustrations based on observed effects cannot be used to reconstruct the trial's prospective design.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: accidental overdose (5.1%), somnolence (3.6%), seizure (3.0%), gingival hypertrophy (3.0%), lower respiratory tract infection (3.0%).

The safety counts are reported separately from the primary efficacy population summaries. Serious adverse events affected 2 of 33 participants at risk in the low-dose group, 10 of 56 in the high-dose group, and 5 of 39 in the placebo group. Other adverse events affected 25 of 33, 46 of 56, and 30 of 39 participants at risk, respectively. No deaths are reported in any of the three groups.

These are counts of participants with events, not event rates adjusted for duration or repeated events. The at-risk counts listed for safety differ from some efficacy analysis group sizes, so the safety denominators should be retained as reported rather than assumed to match the efficacy summaries. The registry lists accidental overdose (5.1%), somnolence (3.6%), seizure (3.0%), gingival hypertrophy (3.0%), lower respiratory tract infection (3.0%), and gingivitis (3.0%) among the top serious adverse event terms. The record does not assign those term percentages to individual treatment groups in the registry record for this analysis.

General explanation: safety counts are descriptive and can be difficult to compare when exposure duration, event definitions, or follow-up differ. The registry entries do not provide exposure-adjusted rates or detailed event narratives. These counts therefore describe the posted safety experience without establishing causation or permitting a complete comparative safety assessment.

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

The primary results describe the measured percent change in apnea episodes per hour from baseline through week 24 for the two sarizotan dose groups and placebo. The point estimates for both active groups are numerically lower than placebo on that scale. However, the sponsor's 95% confidence intervals include zero, and the sponsor-reported p values are above 0.05. The results therefore do not establish a statistically clear difference between either dose group and placebo for this endpoint.

That conclusion is narrower than saying the groups are identical or that no effect is possible. The intervals allow a range of contrasts, including no difference and effects in either direction. They are not precise enough to identify a single effect size, and the registry does not report a threshold for clinical importance. Statistical uncertainty and clinical meaning are related questions, but neither can be settled by the point estimate alone.

The findings apply to the posted primary outcome, analysis population, and period. They do not establish effects on all respiratory symptoms, other features of Rett syndrome, the caregiver-rated outcome, or the open-label treatment phase. The registry describes an open-label phase of up to 168 weeks for patients without safety and tolerability issues, but the primary result timeframe is through week 24. Long-term efficacy cannot be inferred from the blinded-period endpoint.

The record's status is terminated, but the reason for termination is not reported in the registry record. The registry entries do not establish that termination was caused by efficacy, safety, recruitment, or any other specific factor. Likewise, the posted results do not by themselves establish how the outcome would vary in other populations or settings. The appropriate reading is a trial-specific description: the primary analysis did not show a statistically significant difference from placebo, while the intervals leave meaningful uncertainty about the size and direction of any difference.

18. Why This Trial Matters Statistically

This trial illustrates why the effect estimate, its uncertainty, and the analysis method need to be considered together. The primary point estimates are on the lower side of placebo numerically, but the sponsor's confidence intervals cross zero and the reported tests are not statistically significant at 0.05. Reading only the direction of a point estimate could overstate what the results establish; reading only the p value could hide how wide the range of compatible effects remains.

It also demonstrates the difference between a trial's reported model and a recalculation from group summaries. The sponsor used mixed models, while the simple recalculations use posted arm-level estimates and approximate uncertainty. Their broad interpretation is similar, yet their exact intervals and p values differ. That is a reminder that summary-statistic recalculations are analytical checks, not a substitute for the prespecified or sponsor-reported model.

The endpoint presents a practical measurement challenge: respiratory events were monitored at home and summarized as a percent change in counts per hour. Statistical interpretation depends not only on the chosen model but also on recording completeness, variability, and endpoint construction. The registry provides the general measurement description, but not all operational details needed to assess those features.

Finally, the record makes clear that sample-size planning illustrations based on an observed effect are not the same as the trial's original justification. They show how assumed effect size and power targets relate to participant requirements under stated planning assumptions. They cannot establish whether the study was adequately planned or retrospectively powered. These distinctions are central to transparent interpretation of clinical trial results.

19. Limitations

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

Several trial-specific details needed to evaluate the primary result are not reported in the registry record. The full mixed-model specification, covariates, missing-data strategy, and sensitivity analyses are not given. Although the efficacy population is defined as all randomized patients, the record details do not state how many participants contributed usable week-24 monitoring data or how incomplete recordings were handled.

The outcome is based on home monitoring with BioRadio, but detailed procedures for recording quality, invalid data, or episode classification are not reported. The primary outcome is a percent change in apnea episodes during awake time; the registry does not report a threshold for a clinically important difference. Thus, statistical estimates can be described, but the clinical meaning of a particular numerical contrast is not fully anchored by the record.

The registry does not report the original sample-size assumptions or a multiplicity strategy for the two dose comparisons and secondary outcome. It also does not report interim analyses or stopping rules. The study is marked terminated, but the reason is not stated. Those omissions prevent conclusions about whether the trial ended as planned, how its enrollment target was set, or whether analysis choices were influenced by interim findings.

The results summarized concern the blinded period through week 24. The registry describes an open-label phase of up to 168 weeks for eligible participants, but the registry entries available do not include its results or participation. The posted safety counts are descriptive, and detailed exposure-adjusted comparisons are not reported. Finally, the unadjusted recalculations depend on summary statistics and, for the primary outcome, an approximate conversion from standard errors. They are useful for checking the broad pattern but have limitations relative to participant-level analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of the Efficacy, Safety, and Tolerability of Sarizotan in Rett Syndrome With Respiratory Symptoms — NCT02790034.
• Registry record last updated 2021-12-21; status last verified 2021-11.
• Results first posted 2021-12-21.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a randomized, quadruple-masked, parallel-group phase 2 and phase 3 study of sarizotan in patients with Rett syndrome and respiratory symptoms. It enrolled 129 participants and compared low-dose sarizotan, high-dose sarizotan, and placebo. The primary outcome was percent change in apnea episodes per hour during awake time from baseline through week 24, measured through home monitoring.

The sponsor's mixed-model estimates for both dose comparisons have 95% confidence intervals that include zero, and their p values are above 0.05. The unadjusted recalculations lead to the same broad interpretation. One caregiver-rated secondary outcome is posted. Safety summaries report serious and other adverse events by group and no deaths. The registry status is terminated; the reason is not reported in the registry record.