REPOSE Study: Reducing Delirium by Enhancing Postoperative Sleep With Suvorexant: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for REPOSE Study: Reducing Delirium by Enhancing Postoperative Sleep With Suvorexant (NCT05733286), a randomized phase 2 study. The primary outcome is Total Sleep Time (TST) on the First Postoperative Night.

2. Clinical Question

3. Trial Design

The REPOSE study is listed as a phase 2, randomized, triple-masked, parallel-group trial sponsored by Duke University. It compares suvorexant 20 mg with placebo in older surgical patients. The trial status is completed. The registry lists enrollment as 142, while the primary endpoint results include participants with EEG data: 62 in the suvorexant arm and 55 in the placebo arm. These are different descriptions of the study population: enrollment is the trial-level registry figure, and the endpoint analysis is restricted to participants with EEG data.

The record gives a start date of 2023-06-28 and a primary completion date of 2025-06-25. It describes the intended clinical focus as postoperative sleep and delirium severity in adults aged 65 years and older undergoing non-cardiac surgery. The listed primary endpoint is total sleep time on the first postoperative night that a participant received study drug. The record does not describe the masking procedures in detail, identify which roles were masked, or explain how allocation was generated or concealed.

The registry lists seven outcome measures and two analyses. It identifies peak postoperative delirium severity as a secondary outcome, but the posted results in this record include the primary sleep endpoint and do not give a numerical result for delirium severity. The full protocol, original sample-size justification, and detailed analysis plan are not reported in the registry record. Consequently, the posted information supports a description of the design and primary endpoint comparison, but not a complete reconstruction of every planned study procedure or analysis.

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: 14 participants were never assigned to a treatment arm due to screen fail (n= 4), withdrawal by PI (n = 4), subject chose to withdraw prior to surgery (n = 3), and surgery cancellation (n =3).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants with EEG data for total sleep time determination.

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: Participants who received a dose of study drug or placebo.

6. Primary Endpoint

The registry lists the primary outcome as Total Sleep Time (TST) on the First Postoperative Night, measured over The first postoperative night that the participants received study drug (D0).

The primary endpoint is total sleep time (TST), measured in hours by electroencephalography (EEG) on the first postoperative night that participants received study drug, identified in the record as D0. TST is the amount of time spent asleep during the lights-out period, defined in the registry as between 21:00 and 06:00. The reported endpoint population consists of participants with EEG data for determining TST.

Sleep duration is a direct measure of the sleep outcome that the study is designed to examine. Using EEG provides a recorded measure of sleep during the specified overnight period; the registry does not give further details about EEG scoring, device procedures, or how incomplete recordings were handled. Reporting the endpoint as a mean with a standard deviation describes both the average sleep duration and the observed spread of values among analyzed participants.

The primary endpoint is sleep time, not delirium severity. Although the study description also focuses on delirium and the registry lists peak postoperative delirium severity as a secondary outcome, a numerical result for that secondary outcome is not reported in the registry record. The posted primary comparison therefore addresses the recorded sleep-duration measure and should not be read as a numerical comparison of delirium outcomes.

7. Results Posted in the Registry

• Suvorexant Arm: mean 3.91 versus 3.84 on control; difference 0.07 (95% CI -0.67 to 0.81), standardized effect d = 0.03; z-test p = 0.853.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is continuous: each analyzed participant contributes a duration measured in hours, and the registry reports a group mean and standard deviation. A difference in means is a natural summary when the question concerns average sleep duration in two parallel groups. The reported contrast is defined as the suvorexant mean minus the placebo mean, so a positive estimate indicates a higher observed mean in the suvorexant group and a negative estimate indicates a higher observed mean in the placebo group.

What does the two-sided t-test assess?

The registry reports a two-sided t-test. In general, a t-test evaluates whether the observed difference between group means is sufficiently unusual under a model in which the population means are equal. A two-sided test considers departures in either direction, rather than testing only for a higher mean in one named group. Its p-value is a measure of compatibility between the observed data and the null model, conditional on the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the probability that an intervention will produce a particular outcome for an individual.

The reported p-value is 0.853. Considered on its own, that value does not indicate strong evidence against the null model of equal means. It also cannot demonstrate exact equivalence. Establishing that any difference is sufficiently small for a defined purpose would require an equivalence or non-inferiority framework and a prespecified margin; such a margin is not reported in the registry record.

What do the mean and standard deviation describe?

The mean gives the arithmetic average of the recorded sleep durations in each analyzed arm. The standard deviation describes how dispersed individual observations are around that arm’s mean. It is not the uncertainty in the mean itself. The registry reports means of 3.91 hours and 3.84 hours, with standard deviations of 2.0 hours and 2.07 hours. The substantial spread relative to the observed difference is one reason the group means alone should not be interpreted as a precise estimate of the treatment contrast.

General statistical context: a mean-based test is most straightforward when observations are independent and the sampling distribution of the mean difference is adequately approximated by the model used for inference. The registry gives the test type but does not report diagnostic checks, transformations, covariate adjustment, or other modeling details. It is therefore not possible to determine from this record whether additional analytic considerations were used.

How should the confidence interval be read?

A confidence interval describes a range of values compatible with the data under the method used to calculate it. The unadjusted recalculation gives an interval of approximately -0.670 to 0.810 hours for the mean difference. Since the interval spans zero, the data are compatible with no mean difference as well as with differences favoring either arm. The interval’s width also shows that the estimated contrast is not precise enough to tightly locate the underlying difference.

General statistical context: the confidence level refers to the long-run performance of the interval-generating procedure under its assumptions; it is not a probability statement about the fixed treatment effect after observing this particular interval. The confidence level for an interval is not specified in the registry result. The recalculation is an unadjusted summary-based analysis and should be distinguished from the sponsor’s reported test.

What is and is not adjusted for?

The posted comparison is described as a t-test, 2 sided, and the registry gives no covariates or adjusted effect estimate for this endpoint. The displayed mean difference and interval are unadjusted comparisons based on the arm-level summaries. No information in the registry record establishes whether the original analysis included other adjustments beyond what is described in the posted result. The analysis population is stated as participants with EEG data for total sleep time determination; a detailed account of missing observations and exclusions is not reported in the registry record.

General statistical context: adjustment can account for prespecified factors and sometimes improve precision, while an unadjusted comparison is a direct contrast of the observed groups. Whether adjustment is appropriate depends on the design and analysis plan. Without a fuller analysis plan, the recalculation should be treated as a descriptive statistical check rather than a complete reanalysis of the trial.

10. Confidence Intervals and Precision

The observed mean difference in total sleep time was 0.07 hours, with suvorexant minus placebo as the direction of comparison. The recalculated unadjusted confidence interval is approximately -0.670 to 0.810 hours. This interval crosses zero, so the posted data do not sharply distinguish a positive mean difference from a negative one or from no difference.

Precision concerns how narrowly the data locate the effect estimate. Here, the interval covers a meaningful range on both sides of the point estimate, so the estimate should not be treated as a precise measurement of the underlying difference. The group standard deviations, 2.0 hours for suvorexant and 2.07 hours for placebo, are large relative to the difference between the observed means. That spread is relevant because individual sleep durations vary around their group averages.

The interval is a recalculation from posted summary statistics, not a confidence interval reported by the sponsor. The registry provides the sponsor’s p-value but does not report a confidence interval for the primary mean difference. The registry record does not state the confidence level used for a sponsor interval, nor does it report a clinically important difference threshold for TST. Without such a threshold, statistical precision cannot be translated into a conclusion about whether the range of plausible effects is important in clinical terms.

General statistical context: a confidence interval is useful because it shows both the direction and the range of effect sizes compatible with the data under the calculation method. It should be considered alongside the endpoint definition, analysis population, and assumptions, rather than interpreted as a stand-alone decision rule.

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 planning figures are expressed as participants per arm, not total events. They are illustrations based on the observed effect and are not the trial’s original design assumptions. 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 set to the stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the planning calculation indicates would be needed for an 80% chance of detecting the specified effect under the listed assumptions, if that effect were the true one and the model assumptions held. The 90% power column uses a higher target chance of detecting that effect, so it calls for more participants per arm. For planning at 100% of the observed effect, the figures are 13,244 per arm for 80% power and 17,729 per arm for 90% power. For planning at 75% of the observed effect, they are 23,544 and 31,518 participants per arm. For planning at 50% of the observed effect, they are 52,973 and 70,915 participants per arm.

Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm when the effect to detect is reduced. These figures are not observed power. They are prospective planning illustrations calculated from the observed effect, not estimates of the probability that this completed trial detected an effect. The original sample-size rationale and design assumptions are not reported in the registry record.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.070; pooled standard deviation σ = 2.033.
2. n = 2 × (1.96 + 0.842)² × 2.033² / 0.070² = 13,243.1, rounded up to 13,244 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 <- 0.0700000000000003                      # observed difference in means
sigma <- 2.03316972494546                     # 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(5733286)
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 = 13,244 (80% power), 17,729 (90% power)
 75% of observed effect: n per arm = 23,544 (80% power), 31,518 (90% power)
 50% of observed effect: n per arm = 52,973 (80% power), 70,915 (90% power)
power.t.test: 13244 
Simulated power at n = 13,244 per arm: 0.799 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The sponsor’s posted analysis is a two-sided t-test and reports p = 0.853. The unadjusted recalculation from the posted means, standard deviations, and analyzed group sizes also gives p = 0.853. The registry record does not flag a discrepancy between the sponsor’s result and the recalculation.

The recalculation adds an unadjusted estimate of the mean difference, 0.07 hours, and an approximate confidence interval from -0.670 to 0.810 hours. The sponsor’s posted analysis does not give an effect estimate or confidence limits in the record. The recalculation is therefore a summary-statistics check and should not be treated as a more authoritative analysis than the sponsor’s own result. The sponsor’s reported analysis takes precedence when describing the trial’s formal posted analysis; the recalculated interval offers additional context about the estimate’s precision.

The registry does not provide participant-level data or enough detail to reproduce other possible features of the sponsor’s analysis, such as handling of missing EEG data or any model adjustments. Agreement in the reported p-value does not answer those questions or establish that every analytic choice can be independently verified from the registry record.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists seven outcome measures and two analyses, and it names peak postoperative delirium severity as a secondary outcome. The posted numerical result described in the primary analysis is total sleep time on the first postoperative night. A numerical result for the named delirium outcome is not reported in the registry record. The record does not give results for the other listed measures in the registry record for this analysis.

Multiplicity arises when several outcomes, comparisons, or analyses are considered. In general, testing multiple hypotheses can increase the chance of obtaining at least one apparently notable result by chance. Prespecified outcome hierarchies, adjustment procedures, or other strategies can address this concern, but the registry record does not report whether any multiplicity adjustment was planned or applied. The reported p-value should therefore be read as the result for the stated primary comparison, not as evidence that all study outcomes were tested under a single familywise error strategy.

The registry identifies the endpoint population as participants with EEG data for TST determination. It does not report the number or reasons for missing EEG observations, how missing data were handled, whether any imputation was used, or whether sensitivity analyses were performed. It also does not report a complete accounting of randomized participants by analysis population or explain whether the primary analysis followed an intention-to-treat principle.

These omissions matter because the endpoint result is based on a subset with available EEG data rather than the enrollment figure alone. If availability of EEG data were related to group assignment or sleep outcomes, the analyzed groups could differ from the full randomized groups in ways not captured by the posted means. That possibility cannot be assessed from the registry record. Details of outcome definitions beyond the stated TST description, analysis populations for secondary outcomes, and handling of protocol deviations are also 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypotension (3.5%), atrial fibrillation (1.8%), cardiac arrest (1.8%), erythematous rash (1.8%), postoperative seroma infection (1.8%).

The serious adverse event figures are reported separately by arm. In the suvorexant arm, 66 participants were listed as at risk and 9 as affected by serious adverse events. In the placebo arm, 57 were listed as at risk and 9 as affected. The record also lists deaths as 1 in the suvorexant arm and 0 in the placebo arm. These are descriptive registry counts, not an adjusted comparison or an estimate of causal effect.

The record lists the following serious adverse event terms and percentages: Hypotension, 3.5%; Atrial Fibrillation, 1.8%; Cardiac Arrest, 1.8%; Erythematous rash, 1.8%; Postoperative Seroma Infection, 1.8%; and Urinary tract infection, 1.8%. The listed percentages should be read as registry-reported values; the information available does not specify a full event-level breakdown by arm for each term.

Serious adverse event counts do not by themselves establish whether an event was caused by study drug. The registry record does not provide the timing, duration, severity grading, relatedness assessments, or detailed arm-specific event narratives needed for a fuller safety interpretation. It also does not give a comparative statistical analysis of these safety outcomes. The figures describe what the record reports and should not be treated as a complete safety profile.

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

The primary result describes mean EEG-measured sleep duration during the specified lights-out period on the first postoperative night participants received study drug. The observed group means were 3.91 hours for suvorexant and 3.84 hours for placebo, and the estimated mean difference was 0.07 hours. The reported p-value was 0.853, and the recalculated interval extends from approximately -0.670 to 0.810 hours.

These data show that the observed group means were close, while the interval indicates uncertainty about the underlying difference. The result does not establish that the true means are identical, and it does not precisely determine the direction or size of any difference. It also does not identify whether a difference would be clinically important, because a threshold for clinical importance is not reported in the registry record.

The trial’s broader stated purpose includes delirium severity, but the posted primary result is sleep duration. Peak postoperative delirium severity is listed as a secondary outcome, and a numerical result for it is not reported in the registry record. The primary sleep comparison therefore cannot answer whether delirium severity differed between the groups. Nor can the sleep result alone establish effects on other outcomes or on patients outside the endpoint analysis population.

Interpretation is also limited by the endpoint population, which includes participants with EEG data. The registry does not explain the availability of EEG data or how missing data were handled. The posted result is a statistical comparison of the analyzed groups, not a treatment recommendation or a conclusion about what an individual patient should receive.

17. Why This Trial Matters Statistically

This trial raises a useful statistical distinction between a study’s clinical motivation and the endpoint used for its primary comparison. The study description concerns postoperative sleep and delirium severity, while the primary endpoint is objectively recorded sleep duration on a specified night. Keeping these outcomes separate prevents a primary sleep result from being mistakenly treated as a result about delirium.

The trial also illustrates why an effect estimate and its uncertainty are more informative than a p-value alone. The mean difference is 0.07 hours, while the recalculated interval spans values below and above zero. The p-value, 0.853, does not quantify the size of a possible effect or establish equivalence. The interval makes the uncertainty around the observed contrast more explicit.

Another important issue is the analysis population. The trial enrollment figure is 142, whereas the primary endpoint is reported among participants with EEG data. Clear accounting of outcome availability and analysis populations is essential for judging how well a result represents the randomized groups. The registry record does not provide the missing-data details that would help assess that question.

Finally, planning calculations based on an observed effect are not the same as the trial’s original sample-size rationale and do not describe observed power. Distinguishing design assumptions, reported analyses, and retrospective illustrations helps readers avoid treating a planning scenario as evidence about the completed trial’s probability of success. The registry’s limited posted outcome information also makes the distinction between the primary sleep question and the listed secondary delirium question especially important.

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 primary endpoint analysis is restricted to participants with EEG data, and the registry record does not explain why EEG data were unavailable for other enrolled participants. It does not describe missing-data handling, exclusions, imputation, or sensitivity analyses. As a result, the representativeness of the analyzed endpoint population cannot be assessed from the posted information alone.

The primary outcome is specific to the first postoperative night on which participants received study drug. The record does not provide a numerical result for later sleep measurements or explain whether the endpoint captures sleep across subsequent postoperative nights. The registry also does not provide a numerical result for peak postoperative delirium severity, despite listing it as a secondary outcome. This leaves the study’s delirium-focused question unanswered by the posted primary result.

Further details are not reported in the registry record, including the original sample-size justification, the full statistical analysis plan, the confidence level for any sponsor interval, the method for handling multiple outcomes, and whether covariate adjustment or sensitivity analyses were used. The record identifies triple masking but does not explain who was masked or how masking was maintained. These details would be needed to assess additional sources of bias and the full analytic approach.

The posted safety information gives serious adverse event counts and selected event terms, but it does not provide detailed timing, relatedness, severity, or complete arm-specific information for each listed term. The registry results therefore support a focused reading of the primary sleep comparison, rather than a comprehensive assessment of all trial outcomes or safety data.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: REPOSE Study: Reducing Delirium by Enhancing Postoperative Sleep With Suvorexant — NCT05733286.
• Registry record last updated 2026-01-15; status last verified 2025-12.
• Results first posted 2026-01-15.
• 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

The registry record describes a completed phase 2, randomized, triple-masked, parallel-group comparison of postoperative suvorexant 20 mg and placebo in older adults undergoing non-cardiac surgery. Enrollment is listed as 142. The primary endpoint is EEG-measured total sleep time on the first postoperative night participants received study drug, among those with EEG data.

Mean TST was 3.91 hours in the suvorexant arm and 3.84 hours in the placebo arm. The reported mean difference was 0.07 hours, and the sponsor’s two-sided t-test gave p = 0.853. The unadjusted recalculated interval is approximately -0.670 to 0.810 hours. A numerical result for the listed secondary outcome, peak postoperative delirium severity, is not reported in the registry record.