A Study to Evaluate the Respiratory Safety of Lemborexant in Adult and Elderly Participants With Moderate to Severe Obstructive Sleep Apnea, and in Adult and Elderly Participants With Moderate to Severe Chronic Obstructive Pulmonary Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Respiratory Safety of Lemborexant in Adult and Elderly Participants With Moderate to Severe Obstructive Sleep Apnea, and in Adult and Elderly Participants With Moderate to Severe Chronic Obstructive Pulmonary Disease (NCT04647383), a randomized phase 1 study. The primary outcome is OSA Cohort: Apnea-Hypopnea Index (AHI) on Day 8 of Treatment Periods 1 and 2.

2. Clinical Question

3. Trial Design

The registry describes a Phase 1, randomized, double-blind, placebo-controlled, two-period crossover study. It enrolled 63 participants across OSA and COPD cohorts. Each cohort had sequences in which participants received placebo followed by lemborexant 10 mg, or lemborexant 10 mg followed by placebo. Treatment was taken at night from Day 1 through Day 8 of each period. The sequence descriptions specify a washout period of 14 days between treatment periods.

The crossover design means that treatment order varied: participants in one sequence received placebo first, while those in the other received lemborexant first. In principle, comparing the two treatments within the same participant can account for stable individual differences. Whether the posted primary analysis used a paired or period-adjusted model is not reported in the registry record, so the design alone does not establish how those features were handled statistically.

The study was completed. The registry lists a start date of 2021-01-06 and a primary completion date of 2022-02-10. The posted primary outcome concerns AHI on Day 8 in the OSA cohort. The COPD cohort’s outcomes include peripheral oxygen saturation during total sleep time (TST), and secondary outcomes include additional respiratory measurements in both cohorts. The registry record does not report the original design assumptions for the sample size or a detailed statistical analysis plan.

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 48 participants for the obstructive sleep apnea (OSA) cohort were screened, of which 15 were screen failures and 33 were randomized in OSA cohort to receive study treatment. A total of 108 participants were screened for the chronic obstructive pulmonary disease (COPD) cohort, of which 78 were screen failures and 30 were randomized in COPD cohort to receive study treatment.

Treatment Period 1 (8 Days)

Washout Period (14 Days)

Treatment Period 2 (8 Days)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The pharmacodynamic (PD) analysis set for each cohort was the group of participants who had sufficient PD data to derive at least 1 primary PD parameter. Here, "overall number of participants analyzed" signifies those participants who were evaluable for this outcome measure.

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: The safety analysis set for each cohort was the group of participants who received at least 1 dose of study drug and had at least 1 post-dose safety assessment.

6. Primary Endpoint

The registry lists the primary outcome as OSA Cohort: Apnea-Hypopnea Index (AHI) on Day 8 of Treatment Periods 1 and 2, measured over Day 8 of Treatment Periods 1 and 2 (up to Day 30).

The primary endpoint is the mean AHI on Day 8 of treatment periods in the OSA cohort, expressed as apnea and hypopnea events per hour of sleep. The registry defines AHI as the number of apneas and hypopneas divided by total sleep time in minutes and multiplied by 60. Sleep time was measured using polysomnography. This measure expresses the frequency of breathing events relative to time asleep, rather than simply counting events without regard to sleep duration.

AHI is used to describe the frequency of obstructive breathing events during sleep. The registry classifies AHI of 5 to less than 15 as mild, 15 to less than 30 as moderate, and 30 or more as severe. Those categories describe the measure; the posted group means do not indicate how individual participants were distributed across severity categories.

The endpoint’s timing, Day 8, targets measurement after several nights of treatment within a period. The primary outcome record reports group means and standard deviations for placebo and lemborexant 10 mg, along with a mean difference and confidence interval. This outcome addresses the OSA cohort; it should not be taken as the primary result for the COPD cohort, whose respiratory safety outcomes include oxygen saturation.

7. Results Posted in the Registry

• OSA Cohort: Lemborexant 10 mg: mean 44.90 versus 45.09 on control; difference -0.19 (95% CI -11.16 to 10.78), standardized effect d = -0.01; z-test p = 0.973.

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.

OSA Cohort: AHI on Day 1 of Treatment Periods 1 and 2

• 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:
  • OSA Cohort: Lemborexant 10 mg: mean 41.64 versus 44.65 on control; difference -3.01 (95% CI -14.40 to 8.38), standardized effect d = -0.13; z-test p = 0.604.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OSA Cohort: Lemborexant 10 mg and the control. The interval gives the range of effects that remain compatible with the data.

COPD Cohort: Peripheral SpO2 During TST on Day 1 of Treatment Periods 1 and 2

• 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:
  • COPD Cohort: Lemborexant 10 mg: mean 91.13 versus 91.53 on control; difference -0.40 (95% CI -1.67 to 0.87), standardized effect d = -0.16; z-test p = 0.536.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between COPD Cohort: Lemborexant 10 mg and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes extend beyond the primary OSA Day 8 AHI endpoint. They include OSA measurements of AHI and oxygen saturation at other specified times, the time spent below oxygen saturation thresholds, oxygen desaturation index, and counts of desaturations. COPD outcomes include peripheral oxygen saturation and AHI measures. This collection captures different aspects of breathing and oxygenation, and its overall pattern is not reducible to the primary AHI result alone.

The two secondary results with posted numerical summaries are the OSA Day 1 AHI comparison and the COPD Day 1 peripheral oxygen saturation comparison. Their unadjusted intervals include zero. These estimates do not provide precise evidence of a treatment difference, but they also do not establish that the treatments are equivalent. The primary outcome likewise has an interval spanning both directions. In broad terms, the available comparisons do not show a tightly estimated difference; the secondary outcomes add context but do not resolve the primary result’s uncertainty.

The registry lists 10 secondary outcomes, while only two secondary outcomes have posted group summaries and comparisons in the record. The remaining posted outcome titles identify measures, but outcome names alone cannot establish their results. The registry record does not report a complete inferential analysis across the secondary outcomes.

Secondary findings generally carry less weight than a prespecified primary outcome when many measures or time points are examined. Looking across multiple outcomes increases the chance that at least one result may appear notable by chance. The registry record does not report a multiplicity adjustment or a complete prespecified analysis plan, so unadjusted secondary p-values should be treated as exploratory rather than as independent confirmatory evidence. Their value is in describing additional measurements, not in replacing the primary endpoint or establishing a broad conclusion across respiratory outcomes.

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

• OSA Cohort: AHI on Day 1 of Treatment Periods 1 and 2
• OSA Cohort: Peripheral SpO2 During TST on Days 1 and 8 of Treatment Periods 1 and 2
• OSA Cohort: Percentage (%) of TST During Which SpO2 Was <90%, <85% and <80% on Days 1 and 8 of Treatment Periods 1 and 2
• OSA Cohort: Mean Oxygen Desaturation Index (ODI) on Days 1 and 8 of Treatment Periods 1 and 2
• OSA Cohort: Absolute Number of Desaturations (>=3% Reduction From Baseline SpO2) on Days 1 and 8 of Treatment Periods 1 and 2
• COPD Cohort: Peripheral SpO2 During TST on Day 1 of Treatment Periods 1 and 2
• COPD Cohort: AHI on Days 1 and 8 of Treatment Periods 1 and 2
• COPD Cohort: Percentage of TST During Which SpO2 Was <90%, <85% and <80% on Days 1 and 8 of Treatment Periods 1 and 2

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: AHI is measured as events per hour, and the registry reports a mean and standard deviation for each treatment group. A mean describes the arithmetic center of the observations. A standard deviation describes how spread out individual values are around that mean; it is not the uncertainty in the mean itself. The uncertainty in a treatment comparison is instead represented by the confidence interval for the estimated difference.

What does the mean difference represent?

The displayed comparison is the mean for lemborexant 10 mg minus the mean for placebo. Its estimate is -0.19 events per hour. The negative sign indicates that the posted treatment mean was numerically lower than the placebo mean. This is a difference in group averages, not a change experienced by every participant, and it does not describe how many participants improved or worsened. The registry record does not provide participant-level response distributions for this endpoint.

The displayed comparison is an unadjusted recalculation from the posted summary statistics. The discrepancy indicator is false, but the registry record does not report a separate sponsor model or detailed inferential analysis for the endpoint. Because the trial used a crossover design, a full analysis might account for the fact that observations from the same participant are related, as well as period or sequence effects. Whether such terms were included in an original analysis is not reported in the registry record.

Why does the crossover design matter?

In a crossover trial, each participant receives both treatments, usually in a randomized order. A within-participant treatment contrast can reduce the influence of characteristics that remain stable over time, because each participant serves as their own reference. However, measurements from the same person are correlated, so they cannot automatically be treated as if they came from unrelated people. A paired analysis or a suitable repeated-measures model can represent that correlation. The posted group means and standard deviations do not reveal the within-participant correlation, and the analysis approach used by the sponsor is not reported in the registry record.

Period and sequence may also matter in crossover studies. A period effect is a difference associated with when a measurement is made; a sequence effect is a difference associated with treatment order. Carryover is a lingering influence of one period’s treatment into the next. The registry describes a 14-day washout between treatment periods, but the presence of a washout does not by itself show that carryover was absent or that a particular model tested it. The registry record does not report those analyses.

How should the confidence interval and p-value be read?

A confidence interval gives a range of values compatible with the observed data under the interval’s statistical assumptions. For the primary mean difference, the 95% interval runs from -11.16 to 10.78 events per hour. Since it includes zero, the data do not distinguish the estimated direction from no difference at the conventional two-sided 0.05 significance threshold. The unadjusted p-value is 0.973. Neither quantity establishes equivalence: equivalence requires a prespecified margin and an analysis designed to assess whether the uncertainty lies within that margin, neither of which is reported in the registry record.

The p-value is conditional on a statistical model and a null hypothesis. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. The confidence interval is generally more informative about the range and precision of plausible effects, but it too depends on the analysis assumptions. Since the record does not identify a sponsor model for the primary outcome, the unadjusted comparison has to be interpreted with that limitation in mind.

What do spread and over-dispersion mean?

For continuous outcomes such as AHI, the standard deviation describes variability in the measurement. For count outcomes, a count model may need to account for over-dispersion, meaning that variation exceeds what a simple count distribution assumes. This is a general statistical issue; the posted primary endpoint is summarized as a mean and standard deviation, and the registry record does not report a count-model analysis for it. No claim about the adequacy of a specific model can be made from the summary statistics alone.

In general, precision depends not only on the size of the mean difference but also on the variability, amount of information, and analysis structure. In a crossover design, within-person correlation can affect precision, but that correlation is not available in the posted summaries. Accordingly, the group-level recalculation is useful for orientation but cannot recover all information used by a participant-level crossover analysis.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of -0.19 events per hour, with a 95% confidence interval from -11.16 to 10.78. This range is wide relative to the point estimate and includes zero. It permits values in either direction, so the posted result does not precisely identify the direction or size of the difference between the treatment summaries.

A confidence interval is not a range containing a fixed proportion of individual participants’ AHI measurements. It describes uncertainty about an estimated treatment contrast under the assumptions used to calculate it. The standard deviations of 22.85 with placebo and 22.25 with lemborexant 10 mg describe the spread of participant measurements, whereas the confidence interval describes uncertainty around the difference in means. These answer different questions.

The interval’s interpretation depends on the calculation and its assumptions. The displayed estimate is an unadjusted recalculation from posted summaries. Because the study is a crossover, a participant-level analysis could use within-person information that is not recoverable from separate group means and standard deviations alone. The registry record does not report the primary sponsor model, the within-participant correlation, or a prespecified threshold for a clinically important difference.

Consequently, the estimate should not be read as precise evidence of either no difference or a particular effect size. The point estimate is close to zero, but the interval allows a broad range of differences. A nonsignificant p-value does not close that uncertainty or demonstrate equivalence; such a conclusion would require a suitable design and prespecified criteria, which are not reported in the registry record.

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 80% power and participants per arm for 90% power. They are not total enrollment targets and are not observed participant counts. These are continuous-outcome planning illustrations, so the figures refer to participants per arm rather than total events. The planning 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.

The 80% power column gives the illustrative number of participants per arm needed for an analysis to have an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column uses a higher chance of detection and therefore requires a larger planning sample under the same setup. The rows describe planning for 100%, 75%, and 50% of the observed effect. Smaller effects need more participants to distinguish them from random variation, which is why the planning estimates grow as the assumed effect becomes smaller.

These calculations use the observed effect as a starting point, rather than reconstructing the original trial design. The original sample-size assumptions and justification are not reported in the registry record. The displayed figures are planning illustrations, not observed power: they do not measure the probability that the completed trial detected an effect, and they do not alter the uncertainty in the posted treatment estimate. The unusually small observed primary contrast leads to very large illustrative requirements when planning around that contrast, but those figures should not be treated as evidence that the trial’s original design used those targets.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.190; pooled standard deviation σ = 22.546.
2. n = 2 × (1.96 + 0.842)² × 22.546² / -0.190² = 221,033.9, rounded up to 221,034 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.190000000000005                      # observed difference in means
sigma <- 22.5457273406173                     # 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(4647383)
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 = 221,034 (80% power), 295,902 (90% power)
 75% of observed effect: n per arm = 392,950 (80% power), 526,048 (90% power)
 50% of observed effect: n per arm = 884,136 (80% power), 1,183,607 (90% power)
power.t.test: 221034.9 
Simulated power at n = 221,034 per arm: 0.800 (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 identifies a primary OSA outcome and lists multiple secondary outcomes across the OSA and COPD cohorts. Testing many outcomes, time points, thresholds, or cohorts can increase the chance of at least one apparently unusual result even when there is no corresponding underlying effect. Statistical approaches to address this include defining a hierarchy of tests, adjusting significance thresholds, or clearly treating secondary analyses as exploratory. The registry record does not report a multiplicity strategy, so the posted unadjusted secondary comparisons should not be interpreted as if they were protected from the consequences of multiple testing.

The registry reports 12 outcome measures and 0 analyses in its analysis count, while the posted outcome data include primary summaries and a limited number of secondary comparisons. The record does not provide a full statistical analysis plan describing which outcomes were confirmatory, how tests were ordered, or how multiplicity was handled. Those details are not reported in the registry record. The number of outcome measures alone does not establish how many formal hypothesis tests were conducted.

Missing-data handling is also not reported in the registry record. The primary outcome description says the pharmacodynamic analysis set included participants with sufficient pharmacodynamic data to derive at least 1 primary parameter, and that the analyzed number refers to participants evaluable for this outcome. This identifies an evaluability condition but does not explain how missing observations were treated, whether all randomized participants were included in any analysis, or whether sensitivity analyses assessed the effect of missingness.

The registry record also does not report details of the analysis population beyond this endpoint description, such as a full accounting of exclusions or a participant flow for each period. In a crossover study, incomplete participation in one period can affect which within-participant comparisons are available. Without details about the analysis set and missing-data methods, the posted summaries cannot show whether incomplete records could have influenced the comparisons.

These omissions do not demonstrate that the analyses were inappropriate. They limit what can be verified from the registry record. A complete interpretation would require the prespecified analysis methods, the multiplicity plan, and an account of missing outcome data and analysis populations; these are not reported in the registry record.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: radius fracture (3.3%), ulna fracture (3.3%), sars-cov-2 test positive (3.0%).

The registry lists serious adverse events separately by cohort and treatment. In the OSA cohort, the serious-event count was 1 among 33 participants at risk with placebo and 0 among 33 at risk with lemborexant 10 mg. In the COPD cohort, the count was 0 among 30 participants at risk with placebo and 1 among 30 at risk with lemborexant 10 mg. No deaths were listed in these treatment groups.

These are descriptive counts from the registry record. They do not by themselves establish whether an event was caused by treatment, and the small group counts cannot provide a precise comparison of event risk. The record’s top serious-event terms include radius fracture and ulna fracture, each listed as 3.3%, and SARS-CoV-2 test positive, listed as 3.0%. The registry record does not provide enough context in these summary figures to infer a treatment relationship for an individual event.

Serious adverse events are distinct from other adverse events. The posted other-event counts are also listed by group, but interpreting them requires attention to their definitions and reporting. These safety summaries should be read as counts observed during the study, not as proof that a treatment caused or prevented an event.

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

The primary result describes a comparison of mean Day 8 AHI in the OSA cohort. The estimated difference was small relative to the uncertainty interval, and the interval included both lower and higher values for lemborexant compared with placebo. The result therefore does not precisely determine the direction or magnitude of the treatment contrast. It is not evidence of equivalence, and it does not prove that there was no effect.

The study’s clinical question concerned respiratory measurements during treatment, but the posted primary result covers one measure, one cohort, and a specified time point. It does not answer every respiratory safety question in either cohort. The COPD cohort’s oxygen saturation outcomes and the other OSA outcomes are separate measures, and the registry record contains limited posted analyses for those outcomes. The primary result cannot stand in for results that are not reported.

Statistical uncertainty is only one part of interpretation. The record does not state a clinically important difference threshold for AHI, nor does it provide participant-level outcomes or a detailed sponsor model for the crossover analysis. Without those elements, it is not possible to judge whether the interval rules out a clinically meaningful change or how within-participant data affected precision. A p-value that is not statistically significant does not answer those questions.

The posted results also do not establish broader conclusions about all adults or elderly people with OSA or COPD, or about use outside the study conditions. The registry describes a specific Phase 1 crossover study with particular cohorts, treatment, period structure, and outcome times. Generalizing beyond those conditions requires evidence not contained in this record.

Thus, the data can be described as showing closely similar posted group means for the primary endpoint, with substantial uncertainty around their difference. The data do not establish that lemborexant causes no respiratory change, nor do they establish a harmful change. The available record supports a statistical description of these measured outcomes, not a medical recommendation or a definitive judgment about treatment effects.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it uses a crossover design to compare a treatment and placebo in respiratory safety cohorts. In a well-specified crossover analysis, each participant’s observations under both conditions can contribute to the treatment contrast, while accounting for the dependence between measurements from the same person. The public summaries, however, are presented as treatment-group means and standard deviations. They do not disclose the within-participant relationship or the model used to analyze it.

The distinction between a point estimate and its precision is especially important. The primary mean difference is close to zero, but its confidence interval is broad and crosses zero. A reader who focuses only on the point estimate could overstate how firmly the result indicates little difference. A reader who focuses only on the p-value could mistake a lack of statistical significance for evidence of equivalence. The uncertainty interval makes clear that the comparison is not tightly estimated.

The study also illustrates why a registry record’s outcome list and posted numerical results should be distinguished. The record lists a range of secondary respiratory measures, but only a limited subset has posted summaries and comparisons. Without a complete analysis plan and multiplicity strategy, secondary comparisons provide less confirmatory support than a prespecified primary test would.

Finally, the record permits a transparent discussion of planning illustrations without confusing them with the trial’s original design or its observed results. Calculations based on the observed contrast can show how assumed effect size relates to planning requirements, but they do not establish the study’s original sample-size rationale or its achieved power. This separation between design, estimation, and interpretation is central to reading clinical trial statistics responsibly.

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 most important trial-specific limitation is the limited detail about the primary analysis. The study is described as a randomized crossover trial, but the registry record does not report whether the primary comparison accounted for within-participant correlation, period, sequence, or possible carryover. The simple unadjusted recalculation from group summaries cannot recover those design features.

The primary estimate is imprecise: its 95% confidence interval spans values on both sides of zero. The registry record does not report a clinically important difference threshold for AHI, so the interval cannot be judged against a stated clinical margin. It also does not report the original sample-size justification or the assumptions used when planning the trial.

There is limited inferential information for the broader outcome set. The record lists 10 secondary outcomes, but numerical summaries and comparisons are posted for only two secondary endpoints. A complete multiplicity plan and full analysis strategy are not reported in the registry record. This limits interpretation of the wider pattern and makes unadjusted secondary findings less suitable as confirmatory evidence.

The registry describes an analysis set based on sufficient pharmacodynamic data for at least 1 primary parameter, but it does not report detailed missing-data handling, participant flow by period, or sensitivity analyses. These gaps are particularly relevant to a crossover design because a participant may not contribute complete observations from both periods.

Safety summaries are counts by group and provide limited precision for comparing rare events. The posted figures do not establish causality. Finally, the study’s defined cohorts, treatment periods, and respiratory outcomes constrain what can be inferred; the record does not support conclusions beyond these measured settings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study to Evaluate the Respiratory Safety of Lemborexant in Adult and Elderly Participants With Moderate to Severe Obstructive Sleep Apnea, and in Adult and Elderly Participants With Moderate to Severe Chronic Obstructive Pulmonary Disease — NCT04647383.
• Registry record last updated 2023-10-10; status last verified 2022-02.
• Results first posted 2023-10-10.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT04647383 is a completed Phase 1 randomized, double-blind, placebo-controlled crossover study of lemborexant 10 mg in adults and elderly participants with moderate to severe OSA or COPD. The registry lists enrollment of 63 participants, with separate OSA and COPD cohorts and two treatment sequences in each cohort. Treatment was given at night from Day 1 through Day 8, with a 14-day washout between periods.

The listed primary outcome is Day 8 AHI in the OSA cohort. The posted mean difference for lemborexant relative to placebo was -0.19 events per hour, with a 95% confidence interval from -11.16 to 10.78 and an unadjusted p-value of 0.973. The interval is wide and includes zero, so the result is not a precise estimate of the direction or size of a difference. The registry also lists secondary respiratory outcomes and adverse-event summaries, but does not report a detailed primary analysis plan, multiplicity strategy, or missing-data methods.