Study to Assess the Long Term Safety and Tolerability of ACT-541468 (Daridorexant) in Adult and Elderly Subjects Suffering From Difficulties to Sleep: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess the Long Term Safety and Tolerability of ACT-541468 (Daridorexant) in Adult and Elderly Subjects Suffering From Difficulties to Sleep (NCT03679884), a randomized phase 3 study. The primary outcome is Total no. of Subjects With at Least One TEAE.

2. Clinical Question

The clinical question is whether long-term use of daridorexant at 10 mg, 25 mg, or 50 mg is associated with a different frequency of participants experiencing at least one treatment-emergent adverse event than placebo during an extension study in adults and elderly subjects with insomnia disorder. The registry describes the primary objective as assessing long-term safety and tolerability.

This is a safety-focused question, not an assessment of sleep improvement or another efficacy outcome. The registry record lists one outcome measure and does not post secondary outcomes. Consequently, the posted primary outcome can describe event counts across arms, but it cannot by itself characterize the full safety profile or answer questions about symptom benefit.

3. Trial Design

The registry identifies this as a phase 3, randomized, parallel-group study. Its official title describes a multicenter, double-blind, placebo-controlled extension with three daridorexant doses, lasting 40 weeks. The title specifies that it extends studies ID-078A301 and ID-078A302. The record gives an enrollment of 804 and a completed status.

The listed treatment arms are daridorexant 10 mg, daridorexant 25 mg, daridorexant 50 mg, placebo, and Ex-Placebo / Daridorexant 25 mg. Each arm description specifies oral film-coated tablets administered once daily in the evening. The treatment descriptions do not provide further detail about how treatment assignments were implemented.

The registry classifies masking as quadruple, while the official title calls the study double-blind. The record does not explain which roles were masked or reconcile those descriptions. Random allocation is reported, but the allocation ratio and details of the randomization procedure are not reported in the registry record.

The recorded study start date is 2018-10-09, and the primary completion date is 2021-02-22. These dates and the completed status describe the study record; they do not establish when each participant began or finished treatment. For the primary outcome, the timeframe covers TEAEs that started or worsened during the double-blind study period up to 30 days after the double-blind treatment end date, with total duration stated as up to 44 weeks.

The outcome record gives counts of participants with at least one TEAE and the arm denominators, but does not identify an analysis population or explain participant flow into the outcome. The registry record does not report the original sample-size justification or other design assumptions for the trial.

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: Subjects assigned to the daridorexant arms in Study ID-078A301 and 302 received the same dose in the ID-078A303 extension study. Subjects assigned to the placebo arm in Study ID-078A301 and 302 were re-randomized to receive either placebo or 25 mg daridorexant in a 1:1 ratio, with treatment allocation stratified by age into 2 categories (\< 65 and ≥ 65 years). Note: Subjects' demographic and baseline characteristics were collected in the respective confirmatory 12-week study (ID-078A301 or 302).

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.

Population: These are the participants included in the FAS. The discrepancy with previous table (Participant Flow) is due to 3 subjects on FAS (2 on daridorexant 25 mg and 1 on ex-placebo/ daridorexant 25 mg) not starting DB treatment.

6. Primary Endpoint

The registry lists the primary outcome as Total no. of Subjects With at Least One TEAE, measured over TEAEs (AEs that started or worsened during the double-blind study period up to 30 days after double-blind study treatment end date) are reported. Total duration: up to 44 weeks..

The primary endpoint is the total number of participants with at least one treatment-emergent adverse event, or TEAE. The record defines TEAEs as adverse events that started or worsened during the double-blind study period, through 30 days after the double-blind study treatment end date. The stated total duration is up to 44 weeks.

This endpoint is a count of participants, rather than a count of all adverse-event episodes. A participant with multiple TEAEs still contributes to the endpoint as a participant with at least one event. The measure therefore describes whether participants experienced any event meeting the definition; it does not convey the number of events per participant, their duration, intensity, seriousness, or causal relationship to treatment.

Counting participants with at least one TEAE is useful for a broad overview of events arising or worsening during treatment and the specified follow-up window. It is relevant to a study whose stated primary objective is long-term safety and tolerability. However, it is a broad summary measure: distinct clinical events are combined into a single indicator, and the endpoint does not distinguish types of events.

The registry presents this endpoint as counts and explicitly states that no statistical analysis was conducted. It directs readers to the adverse-events information for the full set of safety data. The primary endpoint should therefore be interpreted as a descriptive safety count, not as a stand-alone comparison of the overall safety profiles of the groups.

7. Results Posted in the Registry

• Daridorexant 10 mg: 37.3% (53/142) versus 35.2% (45/128) on control; risk difference 2.2 percentage points (95% CI -9.3 to 13.6), risk ratio 1.06 (0.77–1.46); unadjusted two-proportion z-test p = 0.711.
• Daridorexant 25 mg: 38.4% (103/268) versus 35.2% (45/128) on control; risk difference 3.3 percentage points (95% CI -6.8 to 13.4), risk ratio 1.09 (0.83–1.45); unadjusted two-proportion z-test p = 0.528.
• Daridorexant 50 mg: 40.1% (55/137) versus 35.2% (45/128) on control; risk difference 5.0 percentage points (95% CI -6.7 to 16.6), risk ratio 1.14 (0.84–1.56); unadjusted two-proportion z-test p = 0.402.
• ExPlacebo / Daridorexant 25 mg: 38.1% (48/126) versus 35.2% (45/128) on control; risk difference 2.9 percentage points (95% CI -8.9 to 14.8), risk ratio 1.08 (0.78–1.50); unadjusted two-proportion z-test p = 0.627.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either had at least one TEAE in the defined period or did not. The registry reports the number meeting that definition in each arm. A count is straightforward to interpret, but counts alone are influenced by the number of participants observed in each group. The denominator is therefore essential context. Even with denominators, an unadjusted comparison does not account for differences in follow-up or participant characteristics.

What does a risk difference represent?

A risk difference compares the proportion with the outcome in one arm with the proportion in the reference arm. The posted recalculations use placebo as the reference for the daridorexant dose comparisons and for the Ex-Placebo / Daridorexant 25 mg comparison. A positive estimate indicates a larger observed proportion in the compared arm; a negative estimate would indicate a smaller proportion. A value near zero indicates little estimated difference in the observed proportions. The risk differences reported for this endpoint are 0.022, 0.033, 0.050, and 0.029 for the respective comparisons.

Risk difference is an absolute measure on the proportion scale. It is distinct from a relative measure such as a risk ratio, which expresses one proportion in relation to another. Different measures answer different questions and can give readers different perspectives on the same data. The recalculated relative risks and odds ratios are also posted, but they do not replace the absolute comparison, and none of these recalculations is an analysis reported by the registry as having been conducted for the primary endpoint.

Why are confidence intervals useful?

An estimate from observed participants is subject to sampling uncertainty. A confidence interval gives a range of values compatible with the data under the statistical method used. Narrower intervals indicate more precision, while wider intervals indicate less precision. For a risk difference, zero represents no difference in proportions. All the posted recalculated intervals extend across zero, so the point estimates should not be read as precise evidence of a difference. The interval is not a guarantee that the true value lies within its limits, and its interpretation depends on the method and assumptions used.

How should the p-values be read?

A p-value measures how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the test assumptions held. It does not measure the probability that a treatment has an effect, nor the probability that the null hypothesis is true. The p-values listed for these comparisons are unadjusted recalculations from the posted counts. The registry outcome description says no statistical analysis was conducted, so these values should not be confused with a sponsor analysis or a reported prespecified test.

Multiple comparisons can affect how inferential results are interpreted. The registry record does not report a multiplicity procedure for the primary endpoint. The recalculated comparisons should therefore be viewed as descriptive, separate comparisons rather than as a family of tests with a documented error-control strategy.

What does the endpoint leave out?

The “at least one TEAE” outcome combines event types into a participant-level indicator. It does not distinguish one event from several, or show event duration, severity, seriousness, or relationship to treatment. The separate serious-adverse-event information supplies additional counts, but a count of participants with at least one TEAE is not interchangeable with a serious-adverse-event count. Detailed event categories and the full safety data are relevant for a more complete description.

The registry does not report an adjusted model, details of missing-outcome handling, a formal analysis population, or a detailed statistical analysis plan for this endpoint. It also does not report whether observation time differed across arms. Those omissions constrain interpretation of the unadjusted calculations: they cannot account for information that is not available in the record. The counts and recalculations are best understood as a descriptive comparison based on the posted summaries.

General statistical considerations also matter for binary outcomes. When event proportions are estimated from finite groups, uncertainty depends on both the observed proportions and the amount of information in the groups. If observations are not independent or follow-up differs, simple methods may not represent all sources of uncertainty. The registry record does not describe such complications or report methods addressing them. No assumption about the analysis beyond the stated unadjusted recalculation should be inferred.

10. Confidence Intervals and Precision

The recalculated confidence intervals quantify uncertainty around the risk-difference estimates from the posted counts. For daridorexant 10 mg versus placebo, the estimate is 0.022, with limits -0.093 and 0.136. For daridorexant 25 mg versus placebo, the estimate is 0.033, with limits -0.068 and 0.134. For daridorexant 50 mg versus placebo, the estimate is 0.050, with limits -0.067 and 0.166. For Ex-Placebo / Daridorexant 25 mg versus placebo, the estimate is 0.029, with limits -0.089 and 0.148.

Each interval crosses zero, the value representing no difference in proportions. The estimates point toward higher observed proportions in the compared arms, but the limits also allow for a difference in the opposite direction. The intervals are not narrow enough to support a precise estimate of the size or direction of the difference. This is a statement about the uncertainty in these recalculations, not a conclusion that the groups are equivalent.

Confidence intervals are more informative than a point estimate alone because they show the range of values compatible with the data under the calculation method. Their width reflects statistical uncertainty, but it does not resolve limitations such as missing data, unequal observation time, or unmeasured differences between groups. The registry record does not report an adjusted model or a formal sponsor analysis for the primary outcome. These intervals are unadjusted recalculations, not results of a registry-reported statistical analysis.

The p-values accompanying the recalculated comparisons are 0.711, 0.528, 0.402, and 0.627, respectively. They are unadjusted and should be interpreted alongside the estimates and intervals rather than in isolation. Neither a p-value nor an interval establishes clinical importance, causality, or a complete safety profile.

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 risk difference, not the sample-size requirements stated for the original trial. For this binary outcome, the figures are participants per arm, not total events. Each planning row considers detecting the full observed effect, 75% of the observed effect, or 50% of the observed effect. The columns for 80% and 90% power describe the number of participants per arm required for the planning calculation to have the corresponding probability of detecting the stated effect under its assumptions, if that effect and the assumptions were correct.

The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. These are planning assumptions for the illustration. The trial's own original sample-size assumptions, including its original justification, are not reported in the registry record.

The figures rise as the assumed effect becomes smaller: a smaller difference is harder to distinguish from sampling variation and therefore requires more participants per arm under the same assumptions. For example, the daridorexant 50 mg comparison has planning figures of 1,479 participants per arm for 80% power and 1,980 for 90% power when using 100% of the observed effect; the figures are larger for the rows using smaller fractions of that effect. The corresponding planning figures differ for each comparison because the observed effects differ.

These values are not observed power. They do not describe the probability that the completed study detected an effect, and they do not establish whether the study was adequately designed. They are forward-looking illustrations derived from observed estimates, which themselves are uncertain. The record does not report a trial-specific sample-size plan that would allow the original design rationale to be assessed.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.352; treatment proportion p₁ = 0.373; average p̄ = 0.362.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6798 = 1.3324.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6796 = 0.5720.
4. n = (1.3324 + 0.5720)² / (0.0217)² = 7,718.1, rounded up to 7,719 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
p0 <- 0.3515625                          # control proportion
p1 <- 0.373239436619718                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(3679884)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 7,719 (80% power), 10,332 (90% power)
 75% of observed effect: n per arm = 13,678 (80% power), 18,310 (90% power)
 50% of observed effect: n per arm = 30,673 (80% power), 41,062 (90% power)
power.prop.test: 7718.1 
Simulated power at n = 7,719 per arm: 0.802 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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. Multiplicity, Missing Data and Analysis Populations

The registry outcome description states that no statistical analysis was conducted for the primary endpoint. The posted risk differences, confidence intervals, and p-values are unadjusted recalculations from the summary counts, not a sponsor-reported inferential analysis. The record does not report a prespecified testing hierarchy or a method to control multiplicity across the dose comparisons and the separate Ex-Placebo / Daridorexant 25 mg comparison. Because multiple comparisons may raise the chance of a chance finding when tests are interpreted together, unadjusted p-values should not be treated as confirmatory evidence.

Missing-data handling is not reported in the registry record. The outcome gives arm denominators and counts of participants with at least one TEAE, but the record does not explain whether all participants had complete follow-up, how incomplete observation was handled, or whether participants with missing endpoint information were included in the denominators. The stated TEAE period extends through 30 days after double-blind treatment ends, but the record does not describe how time off treatment or early discontinuation affected observation.

The analysis population is also not reported in the registry record. No information identifies whether the counts refer to all randomized participants, participants who received treatment, or another defined group. The endpoint description does not report an adjusted analysis or a model accounting for participant characteristics or exposure time. Thus the recalculated comparisons are descriptive and should not be interpreted as adjusted treatment effects.

The record lists zero posted analyses for the outcome and does not provide a statistical analysis plan. The original trial sample-size justification, interim-analysis approach, and rules for handling multiple outcomes are not reported in the registry record. Without these details, it is not possible to determine how the outcome and comparisons were intended to fit into the study's original inferential plan.

14. 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: breast cancer (1.4%), aortic valve disease mixed (0.8%), chest discomfort (0.8%), appendicitis (0.8%), cerebrovascular accident (0.8%).

The serious-adverse-event information reports affected participants and the number at risk in each arm. The counts are 5 among 142 for daridorexant 10 mg, 12 among 268 for daridorexant 25 mg, 7 among 137 for daridorexant 50 mg, 2 among 128 for placebo, and 4 among 126 for Ex-Placebo / Daridorexant 25 mg. These figures are counts of participants with a serious adverse event, not counts of all serious-event episodes.

Deaths are listed separately: 1 in the daridorexant 10 mg arm, 1 in the daridorexant 25 mg arm, and 0 in each of the daridorexant 50 mg, placebo, and Ex-Placebo / Daridorexant 25 mg arms. The registry also lists serious-event terms, including Breast cancer at 1.4%, and Aortic valve disease mixed, Chest discomfort, Appendicitis, Cerebrovascular accident, and Head injury at 0.8% each.

These summaries do not establish that treatment caused an event. They also do not describe the full clinical context, duration, or relationship to treatment for each event. Counts across arms should be read with their denominators and alongside the complete safety information; they are not a substitute for the broader TEAE endpoint or a complete safety assessment.

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

The primary endpoint shows how many participants in each arm had at least one TEAE during the stated treatment and follow-up period. The posted counts are useful for describing the observed safety experience in this extension study. The unadjusted recalculations add estimates of between-arm differences, but their confidence intervals cross zero and leave substantial uncertainty about the magnitude and direction of those differences.

These findings do not show that daridorexant caused or prevented adverse events. A treatment-emergent event is defined by when it began or worsened, not by proof that treatment caused it. A causal interpretation would require suitable design and analysis details; the registry record does not report a formal analysis for this endpoint. The recalculated comparisons also do not establish that treatment groups are equivalent or that any difference is clinically important.

The endpoint is broad. It combines all qualifying TEAEs into a count of participants with at least one event and does not distinguish event type, severity, seriousness, or frequency. Serious adverse events and deaths are reported separately, but these figures do not capture the entire safety profile. The registry directs readers to the adverse-events information for the full set of safety data.

This is not an efficacy result. The posted primary outcome does not measure sleep symptoms, treatment benefit, or quality of life. The registry record lists one outcome measure and does not post secondary outcomes. Conclusions about overall benefit and risk cannot be drawn from this endpoint alone.

The study's extension design and the stated follow-up window are also relevant. The record identifies the study as an extension to two earlier studies, but it does not provide enough detail about participant flow, exposure, or missing data to evaluate every potential influence on the comparisons. The appropriate reading is therefore descriptive: the posted counts and recalculations characterize the recorded event data, with important limits on causal and broader clinical interpretation.

16. Why This Trial Matters Statistically

This trial is statistically informative as an example of the difference between a descriptive safety count and a formal comparison. The registry presents a clear participant-level endpoint—at least one TEAE—and arm-specific counts and denominators. Those summaries permit simple unadjusted comparisons, but the outcome description explicitly says that no statistical analysis was conducted. The recalculated estimates and intervals therefore need to remain distinct from sponsor-reported results.

The uncertainty is central to interpretation. Each recalculated risk-difference interval includes zero, and the intervals extend across differences in either direction. The estimates alone might appear to suggest higher observed proportions in the compared arms, but the intervals show that the size and direction of a population difference are not precisely established by these data. Reporting both the estimate and its uncertainty prevents over-reading a point estimate or p-value.

The record also illustrates why broad adverse-event indicators are only one part of safety evaluation. A participant-level “at least one event” endpoint compresses diverse events into a single measure. Serious-event counts, deaths, and individual terms add different information, and none should be substituted for another. In an extension study intended to assess long-term safety and tolerability, these distinctions matter for accurate statistical communication.

Finally, the record does not document the original sample-size rationale, analysis population, missing-data procedures, or multiplicity approach. These gaps limit reconstruction of the planned analysis and the strength of inferential claims. The sample-size illustrations based on observed effects can help explain planning principles, but they are not the original design calculation and are not observed power. Clear separation of recorded findings, recalculations, and unreported methods is essential for responsible interpretation.

17. Limitations

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

The primary outcome description states that no statistical analysis was conducted. Consequently, the arm comparisons discussed for this endpoint are unadjusted recalculations from counts and denominators, rather than results of a reported sponsor analysis. The registry record does not report a formal model, prespecified hypothesis tests, or adjusted estimates.

The record does not specify the analysis population, the handling of missing outcome data, or how incomplete follow-up was treated. It also does not report participant-level exposure time. Although the outcome window is defined as TEAEs starting or worsening during the double-blind period up to 30 days after treatment ends, total duration up to 44 weeks, the record does not explain whether observation varied across participants.

The registry lists five arms, including Ex-Placebo / Daridorexant 25 mg, but the outcome description does not explain the history or role of that group. Allocation ratio and randomization procedures are not reported. The registry labels masking as quadruple, while the official title calls the study double-blind; the record does not clarify which personnel or participants were masked.

The outcome combines all TEAEs into a participant-level count and does not describe event severity, duration, recurrence, or causality. The posted safety figures are therefore not a complete characterization of harms. The record points to the adverse-events information for the full safety data, which is needed to examine event types and additional safety measures.

The original sample-size justification, multiplicity strategy, interim-analysis plan, and detailed statistical analysis plan are not reported in the registry record. The study is described as an extension to earlier studies, but the posted information does not permit evaluation of all participant-flow or carryover considerations. These limitations restrict the conclusions that can be drawn from the primary outcome and the recalculated comparisons.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Study to Assess the Long Term Safety and Tolerability of ACT-541468 (Daridorexant) in Adult and Elderly Subjects Suffering From Difficulties to Sleep — NCT03679884.
• Registry record last updated 2022-03-02; status last verified 2022-02.
• Results first posted 2022-03-02.
• 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.

21. Record Summary

This completed phase 3 study is described as a randomized, parallel-group, placebo-controlled, 40-week extension of studies ID-078A301 and ID-078A302 in adult and elderly subjects with insomnia disorder. The registry reports enrollment of 804 and lists daridorexant 10 mg, 25 mg, and 50 mg, placebo, and Ex-Placebo / Daridorexant 25 mg arms. Treatment is described as oral film-coated tablets administered once daily in the evening.

The primary outcome is the number of participants with at least one TEAE during the double-blind period through 30 days after treatment ends, with total duration up to 44 weeks. The registry outcome description says no statistical analysis was conducted. Unadjusted recalculations from posted counts show positive risk-difference estimates against placebo, but all reported intervals include zero and leave considerable uncertainty.

The record does not report the original sample-size rationale, analysis population, missing-data procedures, or multiplicity approach. The primary counts should be read as descriptive safety information, not as proof of causation, equivalence, or efficacy.