Lemborexant Shift Work Treatment Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Lemborexant Shift Work Treatment Study (NCT05344443), a randomized phase 4 study. The primary outcome is Daytime Total Sleep Time in Minutes Per Day Collected From the Consensus Sleep Diary.

2. Clinical Question

The study record describes a Phase IV randomized, double-blind, placebo-controlled study of a dual orexin receptor antagonist in shift workers. Its stated aim was to test whether lemborexant would increase daytime sleep time compared with placebo. The primary outcome was an average of daily diary measurements over the two-week treatment period, rather than a single-night measurement.

The registry also reports a secondary measure of daytime total sleep time from actigraphy. This allows the posted results to be considered across a diary-based measure and a device-based measure, while keeping the primary question tied to the Consensus Sleep Diary. The registry record does not report additional details about eligibility criteria beyond the condition and population descriptions stated in the study summary.

3. Trial Design

The registry identifies NCT05344443 as a completed Phase IV, randomized, parallel-group study sponsored by the University of California, San Francisco. Enrollment is listed as 29. The study began on 2022-03-10, and its primary completion date is listed as 2024-11-30. These record details describe the study’s administrative status and design; they do not explain why the study was designed with its particular enrollment.

The two arms were Active Treatment and Placebo Treatment. The active arm received lemborexant at 5-10mg, while the placebo arm received a placebo medication described as appearing the same as the active treatment. The registry specifies quadruple masking. The brief summary characterizes the study as double-blind, while the formal masking field records quadruple masking; the registry does not explain the terminology or which roles were masked.

The primary outcome was collected using the Consensus Sleep Diary over two weeks of treatment. The registry reports 14 participants for each arm in the primary outcome summary. It also notes that one participant in the drug condition did not provide any usable diaries for daytime sleep attempts. The secondary outcome used actigraphy and has a different number of participants reported for the placebo arm. The record does not explain the reasons for that difference.

The registry record does not report the original sample-size justification, the planned statistical analysis details beyond the posted mixed-model result, or whether interim analyses were planned or conducted. Those omissions limit what can be inferred about the study’s initial design rationale.

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: Study participants completed baseline assessments, including sociodemographic questionnaires, clinical labs, and sleep measures (diaries, actigraphy) prior to randomization.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Sleep diaries completed during daytime sleep attempts were the source of the treatment data. However, one participant (in the drug condition) failed to provide any useable diaries for daytime sleep attempts

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 Daytime Total Sleep Time in Minutes Per Day Collected From the Consensus Sleep Diary, measured over Two weeks of Treatment.

The primary endpoint is daytime total sleep time in minutes per day, measured with the Consensus Sleep Diary. Participants completed the diary daily, and the registry describes the primary outcome as the average daytime sleep time following a night shift over two weeks of treatment. The reported group values are means, with standard errors as the accompanying measure of spread.

This endpoint addresses the study’s stated question about daytime sleep in workers who sleep during the day after night shifts. A diary can record a participant’s reported sleep experience in the setting the study is concerned with. Averaging diary measurements across the treatment period gives a group-level summary of daytime sleep time, but it also means the summary depends on diary completion and on how the recorded days are handled in the analysis.

The registry notes that one participant in the drug condition had no usable diaries for daytime sleep attempts. It does not report the detailed handling of missing diary entries or the analysis population used for each estimate. The endpoint therefore describes the posted diary-based summary, while its interpretation should take account of the limited reporting about missing observations.

7. Results Posted in the Registry

• Active Treatment: mean 362.70 versus 365.30 on control; difference -2.60 (95% CI -64.14 to 58.94), standardized effect d = -0.03; z-test p = 0.934.

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.

Daytime Total Sleep Time in Minutes Per Day Measured by Actigraphy

• 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 errors.
• Result:
  • Active Treatment: mean 318.40 versus 324.00 on control; difference -5.60 (95% CI -76.21 to 65.01), standardized effect d = -0.06; z-test p = 0.876.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Active Treatment and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome: daytime total sleep time measured by actigraphy. Its broad pattern is consistent with the primary result in that the active-treatment estimate is lower than the placebo estimate, while the reported uncertainty spans both directions. This qualitative alignment does not establish that the diary and actigraphy measure the same aspect of sleep or that they provide independent confirmation.

The secondary outcome is useful as a complementary measurement approach. The primary endpoint comes from participants’ daily Consensus Sleep Diaries, whereas actigraphy is a device-based measure. Agreement in general direction can be informative, but interpretation should consider that the methods may differ in what they capture and in their missingness. The registry does not report a formal analysis combining the two measures.

The actigraphy result has a different number of reported observations by arm than the diary result. The registry does not explain why the placebo count differs or how missing actigraphy data were handled. The reported mixed-model result for the secondary outcome also has uncertainty spanning values in both directions.

Secondary outcomes generally carry less inferential weight than a prespecified primary outcome, particularly when multiple outcomes or analyses are considered. In general, examining multiple results increases the chance of seeing an apparently notable finding by chance unless the analysis plan addresses multiplicity. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting the secondary outcome. Its result is therefore best viewed as supportive descriptive evidence, not as a separate definitive test.

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

• Daytime Total Sleep Time in Minutes Per Day Measured by Actigraphy

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish the observed group summaries from the conclusions that can be drawn from them. The registry reports means for a continuous outcome, standard errors for the arm-level spread, an unadjusted recalculation, and a mixed-model analysis. Each answers a related but different question about the data.

What does a mean difference represent?

A mean is an average of the measured outcome in a group. A mean difference compares the group averages on the same outcome scale. In the primary comparison, the estimate is expressed as active treatment minus placebo: a negative estimate indicates a lower observed mean in the active-treatment group, while a positive estimate indicates a higher observed mean. That sign describes the direction of the estimate, not whether it is statistically persuasive or clinically important.

The primary group means are 362.7 and 365.3 minutes per day. The unadjusted mean difference is -2.6. Because the estimate is derived from the posted summaries, it is a simple comparison and does not necessarily reproduce the model used for the registry’s own analysis. The registry’s mixed-model estimate is -5.9. The study record does not give enough detail about the model specification to determine which features of the repeated measurements or missing data account for the difference between the estimates.

What does a standard error describe?

A standard error describes the statistical uncertainty around an estimated quantity, such as a group mean. It is not the same as the spread of individual participants’ measurements. The registry gives standard errors of 22.0 for the active-treatment group and 22.4 for placebo in the primary outcome. These values help convey the uncertainty in each reported mean, but should not be interpreted as the range of individual sleep times.

In general, repeated measurements from the same participant are related rather than independent. A mixed model can be used to analyze data with such structure, depending on how the model is specified. The registry names Mixed Models Analysis for its reported primary result, but does not report the model formula, covariance structure, assumptions, or missing-data method. It is therefore possible to explain the general role of a mixed model, but not to claim which particular modeling choices were used.

How should the p-value be read?

A p-value measures how compatible the observed data are with a specified statistical null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it is not the probability that the treatment has no effect. The unadjusted recalculation gives p = 0.934, while the registry’s reported mixed-model result gives p = 0.884. These values do not establish that the groups are equivalent. Equivalence requires a prespecified equivalence margin and an analysis designed to evaluate it; such details are not reported in the registry record.

In general, a p-value depends on the estimated effect, its uncertainty, the analysis model, and the assumptions used. A large p-value can occur when an estimated difference is small, when the data are imprecise, or both. The confidence intervals are therefore important alongside the p-values, especially because the intervals include differences in both directions.

Why does the analysis method matter?

The posted recalculation is unadjusted and uses summary statistics for the two arms. The registry’s Mixed Models Analysis is the study’s reported analysis. A model may account for repeated observations or other features of the data, whereas a simple summary-statistic comparison may not. General statistical reasoning cautions against treating these estimates as interchangeable. The registry’s method name alone does not disclose its exact implementation.

The primary outcome summary is based on diary measurements collected daily over the treatment period. Such repeated records can contain within-participant dependence: two diary entries from the same participant may share characteristics. In general, methods that account for this dependence can produce uncertainty estimates different from methods that treat observations as independent. The registry does not state how this dependence was represented in the reported model.

The recalculated p-value and interval should be understood as an unadjusted summary-based comparison, not as a replacement for a fully specified trial analysis. The registry’s own mixed-model result is the appropriate reported trial analysis to cite, while the recalculation offers a transparent comparison based on the posted arm summaries. Neither should be read without its uncertainty interval.

What do the design labels contribute?

Random allocation is intended, in general, to reduce systematic differences between treatment groups at assignment. Masking can reduce the influence of knowledge of assigned treatment on conduct or assessment, depending on who is masked and how masking is maintained. The record labels the study randomized and quadruple-masked, and describes it as placebo-controlled. Those design features do not remove uncertainty from a small study or resolve missing-data concerns.

The study is listed as parallel-group, meaning the arms are presented as separate treatment groups rather than as a crossover comparison in which each participant receives multiple conditions. General interpretation still depends on the actual conduct and analysis. The registry record does not supply further details about allocation procedures, masking roles, or the statistical plan.

11. Confidence Intervals and Precision

Confidence intervals show a range of estimates compatible with the data under the analysis assumptions. A narrower interval indicates greater precision; a wider interval indicates more uncertainty about the size and direction of the difference. An interval is not a guarantee that the true effect lies within its limits, and it does not by itself determine whether a difference matters clinically.

For the reported primary mixed-model analysis, the estimated mean difference is -5.9, with a 95% confidence interval from -88.3 to 76.4. The interval includes negative and positive values, so the estimate is compatible with lower or higher mean daytime sleep time in the active-treatment group. The size of the interval indicates that the result does not pin down the difference narrowly.

The unadjusted recalculation gives a mean difference of -2.6, with an interval from -64.14 to 58.94. This also spans both directions. The recalculated interval and the sponsor’s reported interval differ because they come from different analyses; the registry does not report sufficient model details to explain the difference more specifically. The confidence level is explicitly stated as 95 for the sponsor analysis; the recalculated interval is presented with the posted recalculation, and its confidence level is not separately stated in the registry record.

For the secondary actigraphy analysis, the sponsor-reported interval also includes effects in both directions. The actigraphy summary has fewer reported placebo observations than the diary outcome, and the registry does not explain the difference. Taken together, these intervals are a reminder that estimates from this study remain uncertain. A p-value that does not indicate strong evidence against a null model does not turn a wide interval into evidence of equivalence.

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 expressed as participants per arm, not as total events. The underlying illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as its starting point and shows planning for 100%, 75%, and 50% of that observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the listed assumptions, if that effect and the assumptions were correct. The 90% power column expresses the corresponding planning target for a 90% chance. These are planning calculations, not a description of the study’s observed ability to detect an effect.

For the primary diary outcome, the planning display gives 16,024 participants per arm for 80% power and 21,452 participants per arm for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the corresponding figures are 28,487 and 38,136 participants per arm. For 50% of the observed effect, they are 64,095 and 85,805 participants per arm. The secondary actigraphy planning figures are based on that outcome’s observed effect and are not interchangeable with the primary outcome’s figures.

The pattern illustrates a general planning principle: smaller effects require more participants to detect, all else equal. These are planning illustrations calculated from observed effects, not observed power and not evidence about the trial’s original planning.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Observed difference Δ = -2.600; pooled standard deviation σ = 83.068.
2. n = 2 × (1.96 + 0.842)² × 83.068² / -2.600² = 16,023.6, rounded up to 16,024 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -2.60000000000002                      # observed difference in means
sigma <- 83.0681647804982                     # 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(5344443)
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 = 16,024 (80% power), 21,452 (90% power)
 75% of observed effect: n per arm = 28,487 (80% power), 38,136 (90% power)
 50% of observed effect: n per arm = 64,095 (80% power), 85,805 (90% power)
power.t.test: 16024.6 
Simulated power at n = 16,024 per arm: 0.797 (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 registry’s own primary analysis is a Mixed Models Analysis. It reports a mean difference (net) of -5.9, a 95% confidence interval from -88.3 to 76.4, and p = 0.884. This is the sponsor-reported analysis of the primary outcome and should be distinguished from the unadjusted recalculation based on the posted group summaries.

The recalculation gives a mean difference of -2.6, an interval from -64.14 to 58.94, and p = 0.934. Its estimate and uncertainty differ from the mixed-model result. An unadjusted summary-statistic comparison and a model-based analysis need not produce identical results, particularly when the outcome is measured repeatedly. However, the registry does not provide enough methodological detail to attribute the difference to a specific modeling or data-handling choice.

The discrepancy flag is false. The posted recalculation is therefore a supplementary, unadjusted comparison rather than a correction to the reported analysis. The two results point to estimates near zero relative to their uncertainty, but neither establishes equivalence or excludes differences in either direction. The registry does not report the full statistical analysis plan needed to evaluate the mixed model in greater detail.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, time points, or analyses are examined. In general, the more statistical tests considered, the greater the possibility that at least one result appears notable by chance. A prespecified testing hierarchy or adjustment can help control that problem, but such plans must be known to interpret the set of results correctly.

The registry lists a primary outcome and one posted secondary outcome. It reports two outcome measures and two analyses. The record does not report whether additional outcomes or analyses were planned, whether the secondary outcome was subject to a multiplicity adjustment, or what hierarchy was intended for testing. It is therefore not possible to determine from the registry record how multiplicity was handled.

Missing data are also relevant. The primary outcome description states that one participant in the drug condition did not provide any usable diaries for daytime sleep attempts. For the secondary actigraphy outcome, the reported placebo group size differs from the primary outcome summary. The registry does not explain the reason for that difference or describe the handling of missing actigraphy records. It also does not report imputation methods, sensitivity analyses, or assumptions about why data were missing.

The registry identifies the group summaries and reports mixed-model analyses, but does not state the analysis population definition, such as whether the primary analysis followed an intention-to-treat principle or used another population. The record also does not detail how participants with incomplete observations contributed to the model. These omissions matter because the interpretation of a treatment estimate can depend on which participants and observations were included and on assumptions about unavailable data.

These reporting gaps do not prove that the study failed to address multiplicity or missing observations. They mean that the registry record does not allow readers to assess those procedures in detail. The estimates should be interpreted alongside that uncertainty rather than as if every aspect of the analysis were fully documented.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports serious adverse events for the Active Treatment and Placebo Treatment groups. Serious adverse events affected 0 participants among 15 at risk in the active group and 0 among 14 at risk in the placebo group. The registry also reports 0 deaths in each group. No serious adverse event terms are listed.

For other adverse events, the registry reports 5 affected participants among 15 at risk in the active group and 1 among 14 at risk in the placebo group. These figures are descriptive counts in the registry record; they do not by themselves establish that treatment caused an event or explain its type, severity, timing, or relationship to treatment.

The safety figures should be read in the context of the study’s limited enrollment and the short treatment period described for the primary outcome. The absence of reported serious events in these groups does not establish that serious events cannot occur, and the other-event counts do not identify the clinical significance of the events. The registry record does not provide the event terms for the other adverse events in the registry record reported for this analysis.

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

The posted primary results estimate a small active-minus-placebo difference in average diary-recorded daytime sleep time, while the uncertainty intervals extend across negative and positive values. The registry’s mixed-model analysis and the unadjusted recalculation both leave substantial uncertainty about the direction and magnitude of any difference. The study results therefore do not establish that the groups are equivalent, and they do not precisely determine the size of a treatment effect.

Likewise, the results should not be interpreted as proof that lemborexant either increases or decreases daytime sleep time. The reported estimates are based on a small study enrollment, and the confidence intervals are broad. A point estimate is only one estimate from the observed data; the interval conveys that materially different values remain compatible with the analysis.

The registry’s secondary actigraphy outcome provides a complementary measure, but it does not remove the uncertainty in the primary outcome. Its results have their own missing-data and analysis-reporting limitations, and the record does not describe multiplicity procedures. Consistent direction across endpoints can be noted without treating the secondary measure as independent confirmation.

These are statistical interpretations of the registry results, not medical advice. The record describes one randomized, placebo-controlled study over two weeks of treatment. It does not provide evidence about longer-term outcomes or establish how results would generalize beyond the population described in the registry.

18. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the distinction between an observed estimate and the precision of that estimate. A comparison can produce a point estimate close to zero and a large p-value while still leaving a broad range of plausible effects. The confidence intervals are essential for seeing that lack of a statistically notable result is not the same as evidence of no effect.

The record also permits comparison between the sponsor-reported mixed-model analysis and an unadjusted recalculation from group summaries. The results are not identical, which reinforces why the analysis method matters for repeated diary measurements. The registry names the model but does not give enough detail to reproduce or fully assess its implementation.

Another statistical lesson concerns planning. The sample-size illustrations are based on the observed effect, and their required participant counts increase as the effect targeted for detection becomes smaller. They are planning scenarios, not an account of the original design rationale or of observed power. The registry does not report the original sample-size justification.

Finally, the registry’s reporting of missing diary data, different outcome-specific group counts, and limited details on multiplicity and analysis populations highlights how reporting completeness shapes interpretation. These issues do not invalidate the posted estimates, but they define what can be concluded from the record and what remains uncertain.

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.

The registry record leaves important design and analysis details unreported. It does not give the original sample-size justification, the full statistical analysis plan, or details about any interim analyses. The planning illustrations use observed effects and cannot substitute for the trial’s original rationale.

The reported primary result comes from a mixed-model analysis, but the model specification, covariance structure, assumptions, and missing-data method are not reported. As a result, the sponsor’s estimate cannot be fully reconstructed from the registry record. The unadjusted recalculation is based on posted summaries and is not a substitute for those model details.

Missingness is a specific concern for interpretation. The registry notes one drug-condition participant without usable sleep diaries for daytime sleep attempts, and the placebo group’s reported count for actigraphy differs from its primary outcome count. Reasons for these missing observations, their handling, and sensitivity analyses are not reported. The analysis population is also not stated.

The record does not report how multiplicity was handled across outcomes or analyses. This limits interpretation of secondary results as confirmatory evidence. Further, the posted safety information gives adverse-event counts but does not provide terms for the other adverse events in the registry record.

Finally, the primary endpoint summarizes diary-based daytime sleep over two weeks of treatment. The registry results do not describe outcomes beyond that period. The limited enrollment and broad intervals also mean that estimates remain imprecise. These limitations define the scope of inference from the posted record rather than proving that the underlying trial procedures were inadequate.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Lemborexant Shift Work Treatment Study — NCT05344443.
• Registry record last updated 2026-02-04; status last verified 2026-02.
• Results first posted 2026-02-04.
• 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

NCT05344443 is a completed Phase IV randomized, parallel-group, placebo-controlled study sponsored by the University of California, San Francisco. The registry lists quadruple masking and enrollment of 29. Participants were assigned to lemborexant at 5-10mg or placebo.

The primary outcome was mean daytime total sleep time per day from the Consensus Sleep Diary over two weeks of treatment. The sponsor-reported mixed-model estimate was -5.9, with a 95% confidence interval from -88.3 to 76.4 and p = 0.884. The unadjusted recalculation was -2.6, with an interval from -64.14 to 58.94 and p = 0.934.

The posted estimates are imprecise and do not establish equivalence or a clear direction of difference. The secondary actigraphy result shows a broadly similar pattern, with uncertainty in both directions. Important details about sample-size justification, multiplicity, missing-data handling, and analysis populations are not reported in the registry record.