Safety and Efficacy Study of Suvorexant in Participants With Primary Insomnia - Study B (MK-4305-029): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy Study of Suvorexant in Participants With Primary Insomnia - Study B (MK-4305-029) (NCT01097629), a randomized phase 3 study. The primary outcome is Suvorexant HD Versus Placebo: Change From Baseline in Mean Subjective Total Sleep Time (sTSTm) at Month 1.

2. Clinical Question

The primary endpoint focuses on participants’ reports of sleep duration rather than a laboratory measurement. The Month 1 measure averages available diary observations in the Days 23-30 range, with Day 1 defined as the day of the first double-blind dose. The comparison is expressed in minutes as a difference in least-squares means. A positive difference means the estimated change in the HD group is greater than the estimated change in the placebo group; it does not by itself establish how meaningful that difference is to participants. The registry record does not report a threshold for clinical importance.

3. Trial Design

This was a Phase III, multicenter, randomized, double-blind, placebo-controlled, parallel-group study of MK-4305, identified in the record as suvorexant. The listed condition was primary insomnia. The record reports enrollment of 1020 and a completed study. The study start date is 2010-05-03, and the primary completion date is 2011-11-08.

The intervention groups included suvorexant HD, suvorexant LD, and placebo. The primary hypothesis and primary endpoint analysis concern the HD-placebo comparison, not a pooled comparison across suvorexant doses. The record does not report the allocation ratio or the original planned group sizes. It identifies randomization and double masking but does not give further details about sequence generation, concealment, or which study roles were masked.

The main outcome was change from baseline in mean subjective total sleep time at Month 1. The record defines this as the average of available daily e-diary measurements during Days 23-30, excluding mornings after polysomnography nights. At least 3 days of data within the defined range were required to calculate a day-range average; otherwise, the mean for that range was treated as missing. Baseline was the mean of the last 7 daily measurements in the placebo run-in period.

The primary analysis population is described as randomized participants with baseline data and at least one post-randomization e-diary observation after at least one dose of study drug. The registry record does not report the original sample-size justification, trial-specific power assumptions, interim-analysis plan, or a complete statistical analysis plan. These omissions limit what can be said about the design decisions behind the trial, even though the posted results include a sponsor analysis and outcome estimates.

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 2-week single-blind placebo Run-in occurred prior to randomization. 1 of the 1020 randomized participants enrolled in 2 separate suvorexant trials and is excluded from all summaries and analyses. 10 other randomized participants were not treated and are in Participant Flow Table below, but are excluded from all other summaries and analyses.

Only the first 6 of 8 groups are shown.

Double-Blind (DB) Treatment (TRT) Phase

Reasons for not completing this period:

DB RO Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Randomized participants with ≥1 post-randomization e-diary observation after ≥1 dose of study drug, and baseline data were included in this analysis. The hypothesis included only the suvorexant HD-placebo comparison.

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 Suvorexant HD Versus Placebo: Change From Baseline in Mean Subjective Total Sleep Time (sTSTm) at Month 1, measured over Baseline and Month 1.

The primary endpoint is change from baseline in mean subjective total sleep time (sTSTm) at Month 1, measured in minutes. It represents participants’ reports, entered in a daily electronic diary, of the total time they spent asleep before waking for the day. For the Month 1 value, available measurements within Days 23-30 were averaged. Mornings following polysomnography nights were excluded. The baseline value was the mean of the last 7 daily measurements in the placebo run-in period.

This endpoint is used to assess sleep duration from the participant’s perspective over a defined period, rather than relying only on a single night. Averaging diary observations can reflect repeated reports during that period, while the requirement for at least 3 days of data sets a minimum for calculating the range average. When that minimum was not met, the range mean was considered missing. How missing Month 1 values were handled in the statistical model beyond this rule is not reported in the registry record.

The registry identifies the estimate as a difference in least-squares means. In general, a least-squares mean is a model-based estimate, rather than simply the raw average of all observations. The registry names Longitudinal Data Analysis as the sponsor’s method, but does not describe the model specification or its assumptions. The endpoint gives a quantitative measure of reported sleep duration; by itself, it does not describe all aspects of insomnia or establish whether a change is important to participants. A threshold for clinical importance is not reported in the registry record.

7. Results Posted in the Registry

• Suvorexant HD: mean 48.70 versus 22.40 on control; difference 26.30 (95% CI 18.31 to 34.29), standardized effect d = 0.48; z-test p = <0.001.

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.

Suvorexant HD Versus Placebo: Change From Baseline in sTSTm at Week 1

• 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:
  • Suvorexant HD: mean 40.40 versus 14.00 on control; difference 26.40 (95% CI 19.72 to 33.08), standardized effect d = 0.57; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Suvorexant HD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Suvorexant HD Versus Placebo: Change From Baseline in WASO at Night 1

• 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:
  • Suvorexant HD: mean -63.30 versus -21.30 on control; difference -42.00 (95% CI -48.68 to -35.32), standardized effect d = -1.03; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Suvorexant HD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Suvorexant HD Versus Placebo: Change From Baseline in sTSOm at Week 1

• 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:
  • Suvorexant HD: mean -19.70 versus -6.70 on control; difference -13.00 (95% CI -17.70 to -8.30), standardized effect d = -0.40; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Suvorexant HD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results cover several related sleep measures and assessment periods. They include subjective total sleep time at Week 1, wake time after persistent sleep onset (WASO) at Night 1, and subjective time to sleep onset (sTSOm) at Week 1. The registry also names latency to onset of persistent sleep (LPS) at Night 1 as a secondary outcome, but a numeric LPS result is not reported in the registry record. The result set therefore does not provide a complete numerical account of every named secondary outcome.

Across the posted numeric secondary measures, the reported comparisons favor a greater increase in subjective sleep duration and greater reductions in wake time after persistent sleep onset and reported time to sleep onset in the HD group relative to placebo. The directions align broadly with the primary Month 1 sleep-duration result, while the endpoints and measurement times differ. These outcomes can add context about different aspects of sleep, but they should not be treated as interchangeable measures or as repeated confirmation of the same endpoint.

Each secondary estimate has its own uncertainty and analysis. The secondary results are reported with p-values below < 0.001 by the sponsor, while simple unadjusted recalculations report p-values below 0.001. The registry record does not report whether testing was adjusted for the number of outcomes or comparisons. In general, when multiple outcomes are examined, the chance of obtaining apparently notable results by chance can increase unless the testing strategy is addressed. Unadjusted secondary results therefore carry less confirmatory weight than a prespecified primary analysis, especially when the multiplicity plan is not reported.

The secondary results are best read as supporting context for the specific outcomes and time points recorded, not as proof that all dimensions of sleep changed in the same way or to the same degree. The record does not report a hierarchy for secondary hypotheses or a threshold for meaningful change on these measures. Interpretation should retain the distinction between the primary endpoint and exploratory or otherwise secondary comparisons.

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

• Suvorexant HD Versus Placebo: Change From Baseline in sTSTm at Week 1
• Suvorexant HD Versus Placebo: Change From Baseline in WASO at Night 1
• Suvorexant HD Versus Placebo: Change From Baseline in sTSOm at Week 1
• Suvorexant HD Versus Placebo: Change From Baseline in LPS at Night 1

9. Statistical Interpretation

10. Statistical Methods Explained

What does a difference in least-squares means represent?

The primary result is reported as a difference in least-squares means. In general, least-squares means are estimated group means from a statistical model. A difference between them compares the modeled outcome in the two groups, while accounting for the model terms that were specified. This is distinct from merely subtracting two unadjusted sample averages. The registry names Longitudinal Data Analysis as the sponsor’s method, but the model terms, covariance structure, and other specification details are not reported in the registry record. It is therefore possible to describe the estimand as reported without reconstructing the sponsor’s model.

The reported primary estimate is 26.3 minutes. Its interpretation is the estimated difference in mean change in sTSTm at Month 1 between suvorexant HD and placebo. The positive sign indicates a greater estimated change in the HD group. The endpoint is itself a change from baseline, so the result is a contrast in changes, not a comparison of the groups’ Month 1 values alone. The registry’s description of the primary outcome and the reported analysis both identify Month 1 as the assessment period.

What does the confidence interval add?

A confidence interval expresses uncertainty around an estimated effect. In general, a 95% confidence interval is generated by a procedure that, under its assumptions, would cover the underlying parameter in 95% of repeated applications. It is not a statement that there is a 95% probability that the fixed parameter lies within this particular interval. The sponsor’s interval for the primary difference runs from 18.3 to 34.3 minutes. Its width reflects estimation uncertainty under the sponsor’s analysis, but it does not encompass all sources of uncertainty, such as model misspecification or unreported analysis choices.

The posted recalculation gives a 95% interval from 18.31 to 34.29 minutes. This recalculation uses posted summary statistics and is unadjusted; it is not a substitute for a longitudinal model using participant-level observations. The close alignment of the displayed estimates is informative as a numerical check, but the sponsor’s own analysis remains the main trial analysis. The record marks no discrepancy between the re-calculation and the sponsor result.

Why distinguish sponsor analysis from recalculation?

The sponsor’s analysis is identified as Longitudinal Data Analysis, with the parameter described as a difference in least-squares means. The recalculation is based on group-level summary values and makes simplifying assumptions. In general, summary-statistic recalculations can be useful for checking the direction and approximate magnitude of a reported contrast, but they do not reproduce a model-based analysis unless the required design and model information are available. The record does not provide the full model specification or participant-level data. Thus, the recalculated p-value should be read as an unadjusted check, not as an alternative primary test.

The sponsor reports p < 0.001, while the simple recalculation reports p < 0.001. These are both threshold-formatted values rather than exact p-values. They should not be treated as equal precision statements or used to infer unreported model details. Because the point estimates and confidence intervals are aligned, the central interpretation of the primary contrast is similar across the two presentations; the sponsor’s stated analysis is still the trial’s formal result.

What assumptions shape a continuous-outcome analysis?

For a continuous measure such as minutes of reported sleep, a comparison commonly uses a model or a mean-based procedure. In general, inference depends on the way variability is estimated and on assumptions about the distribution and dependence of observations. Repeated diary observations from the same participant are not necessarily independent. A longitudinal method can account for repeated measurements through its model, but the specific way this was done is not reported in the registry record. No distributional diagnostics or sensitivity analyses are reported in the registry record.

The group-level values include least-squares means, 95% confidence limits, and measures of spread. The recalculation uses an approximate pooled standard deviation and derives a simple unadjusted comparison. Because that standard deviation is marked as approximate, it should be understood as an approximation, not as a direct reproduction of the sponsor’s longitudinal model. General statistical practice treats such calculations as planning or descriptive aids when their assumptions are explicit, rather than as evidence that the original analysis used the same procedure.

How do missing observations matter?

The diary averaging rule requires at least 3 daily measurements in the Month 1 range; without that minimum, the range mean is considered missing. This defines when an endpoint value can be calculated. It does not explain how participants with a missing range mean contributed to the sponsor’s model, whether any imputation was used, or how missingness was assessed. Those details are not reported in the registry record. In general, missing-data methods rely on assumptions about why observations are absent, and results can be sensitive to those assumptions. No additional missing-data strategy should be inferred from the averaging rule alone.

The primary analysis population is described as randomized participants who had baseline data and at least one post-randomization e-diary observation after at least one dose. That wording defines inclusion in the stated analysis but does not give a full participant flow or explain how all randomized participants were treated in the model. The registry record does not report a detailed analysis-population flow for the primary endpoint.

What is the role of the p-value?

In general, a p-value measures the compatibility of the observed data with a null hypothesis, conditional on the statistical model and its assumptions. It does not quantify the probability that the null is true, does not describe the magnitude of the effect, and does not establish clinical importance. The sponsor’s reported primary p-value is below < 0.001; the recalculated unadjusted value is below 0.001. The confidence interval and the estimated difference provide complementary information about magnitude and precision. The registry record does not report whether multiplicity adjustments were used for the primary or secondary analyses.

11. Confidence Intervals and Precision

The sponsor-reported primary difference in least-squares means is 26.3 minutes, with a 95% confidence interval from 18.3 to 34.3. The interval is entirely above zero, the value representing no estimated between-group difference. Under the sponsor’s analysis, the interval therefore supports a positive estimated difference in mean change in sTSTm for the HD group compared with placebo. The interval gives a range of estimates compatible with the analysis; it does not predict the range of individual participants’ outcomes.

The unadjusted recalculation gives a 95% confidence interval from 18.31 to 34.29 minutes. The recalculated point estimate is also 26.3 minutes. These limits are based on the posted group summaries and an approximate standard deviation, whereas the sponsor reports a Longitudinal Data Analysis. The distinction matters: similar numerical results do not make the analyses methodologically identical. The sponsor’s model-based result is the formal reported analysis.

In general, a narrower confidence interval indicates greater statistical precision for the estimated contrast, while a wider interval indicates more uncertainty. Precision is not the same as clinical importance or freedom from bias. A confidence interval reflects sampling uncertainty under a method and its assumptions; it does not account automatically for missing-data bias, selective reporting, multiplicity, or errors in endpoint measurement.

The registry record does not report a threshold for a clinically important difference in sTSTm. Consequently, the interval can be interpreted as describing the estimated effect and its statistical uncertainty, but not as establishing whether the full interval represents changes that participants would consider important. It also applies to the defined Month 1 diary measure and analysis population, rather than to every sleep outcome or every participant group.

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 illustration gives participants per arm for the continuous-outcome comparison; these are not total event counts. It 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 a reference and considers effects at the stated fractions of that observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the modeled participants per arm for a planning scenario designed to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and assumptions held. The 90% power column describes the corresponding planning target for a 90% chance. For the primary endpoint, planning for 100% of the observed effect gives 68 participants per arm for 80% power and 91 participants per arm for 90% power. Planning for 75% of the observed effect gives 120 participants per arm for 80% power and 161 participants per arm for 90% power. Planning for 50% of the observed effect gives 270 participants per arm for 80% power and 361 participants per arm for 90% power.

Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants per arm under these assumptions. These figures are illustrations based on the observed result, not the trial’s original design requirements. They are not observed power: observed power is not a useful substitute for interpreting the estimate and its confidence interval after results are known. The planning values also do not account for design features not included in the stated assumptions, such as any unreported allowance for missing outcomes.

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 = 26.300; pooled standard deviation σ = 54.499.
2. n = 2 × (1.96 + 0.842)² × 54.499² / 26.300² = 67.4, rounded up to 68 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 <- 26.3                      # observed difference in means
sigma <- 54.4991517061355                     # 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(1097629)
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 = 68 (80% power), 91 (90% power)
 75% of observed effect: n per arm = 120 (80% power), 161 (90% power)
 50% of observed effect: n per arm = 270 (80% power), 361 (90% power)
power.t.test: 68.4 
Simulated power at n = 68 per arm: 0.798 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor reports a Longitudinal Data Analysis for the primary HD-versus-placebo comparison. The reported difference in least-squares means is 26.3 minutes, with a 95% confidence interval from 18.3 to 34.3 and p < 0.001. This is the trial’s own analysis and should be treated as the formal result reported by the registry.

The simple recalculation from the posted summary statistics estimates the same displayed difference, 26.3 minutes, with a 95% confidence interval from 18.31 to 34.29 and p < 0.001. It is an unadjusted calculation based on group summaries and an approximate pooled standard deviation. It does not reproduce the sponsor’s longitudinal model. Its role is to provide a check on the broad numerical result, not to replace the planned or reported analysis.

The registry record indicates no discrepancy between the recalculation and sponsor analysis. The different p-value thresholds and slight differences in interval limits should nevertheless be read in light of the different methods and displayed precision. The record does not provide enough model detail to explain the exact differences. The sponsor’s own analysis takes precedence as the trial analysis; the recalculation is supplementary and should not be interpreted as a competing model-based finding.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 14 outcome measures and 12 analyses. It identifies a primary outcome and several secondary outcomes, including additional sleep measures at Week 1 or Night 1. The primary hypothesis is restricted to suvorexant HD versus placebo. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a procedure for controlling the family-wise error rate or false discovery rate across outcomes and comparisons. It is therefore not possible to determine from the record whether the reported secondary p-values were adjusted for repeated testing.

Multiplicity matters because testing several hypotheses can increase the chance that at least one result appears statistically notable even when the underlying effects are absent. In general, prespecifying a primary endpoint and a testing sequence can help distinguish confirmatory evidence from secondary or exploratory findings. Here, the primary endpoint is identified, but the full statistical plan and the treatment of multiple comparisons are not reported in the registry record. The secondary findings should consequently be interpreted with more caution than the primary analysis.

The primary analysis population includes randomized participants with baseline data and at least one post-randomization e-diary observation after at least one dose. For Month 1, the diary average required at least 3 available daily measurements during Days 23-30; otherwise, that range’s mean was considered missing. The registry does not report the number of participants with missing primary outcomes, the reasons observations were missing, or the sponsor’s handling of missing values in the longitudinal analysis. It also does not report sensitivity analyses examining alternative missing-data assumptions.

In general, missing-data methods depend on assumptions about whether the likelihood of missingness is related to observed or unobserved outcomes. The diary rule explains when a range-level value could be calculated, but it is not a complete missing-data method. The record also does not provide a detailed flow from randomized participants to the primary analysis set. These omissions limit assessment of how much missing data may have affected the primary and secondary estimates.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

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: meningitis (0.9%), atrial fibrillation (0.4%), ankle fracture (0.4%), endometritis (0.3%), gastroenteritis (0.3%).

The registry presents serious and other adverse-event counts across treatment-phase, follow-up, and additional groups. During the treatment phase, serious adverse events affected 6 of 387 in the suvorexant HD group, 5 of 383 in the placebo group, and 2 of 239 in the suvorexant LD group. Other adverse events affected 59 of 387, 33 of 383, and 33 of 239, respectively. These are counts of participants affected as reported for the named groups; they are not an adjusted comparison of risk.

Safety entries are separated by group and period, including follow-up and groups labelled after treatment. They should not be combined or treated as mutually exclusive without further information about the registry’s group definitions. Death counts are null in the posted safety data, so death results are not reported in the registry record. The record lists serious-event terms with percentages, including meningitis at 0.9%, atrial fibrillation at 0.4%, ankle fracture at 0.4%, endometritis at 0.3%, gastroenteritis at 0.3%, and bladder neoplasm at 0.3%. It does not provide enough context in these entries to infer comparative rates for each term.

These safety counts are descriptive. The registry record does not report a formal statistical comparison for these adverse-event summaries, and the counts alone do not establish causation or the overall balance of benefits and harms. They should be read in the context of the stated group and period rather than as a complete safety assessment.

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

The posted primary result estimates a greater mean change from baseline in subjective total sleep time at Month 1 for suvorexant HD than for placebo. The sponsor’s estimated difference is 26.3 minutes, with a 95% confidence interval from 18.3 to 34.3. The confidence interval lies above zero under the reported analysis, and the sponsor reports p < 0.001. These figures describe the group-level estimate for the specified diary outcome, time window, and analysis population.

The result does not mean that every participant experienced an increase of 26.3 minutes, or that each person’s outcome was close to the group estimate. It does not describe the distribution of individual responses. The registry record does not report a clinically important threshold for the primary measure, so the statistical estimate alone cannot establish how important the observed difference is to participants.

The result also does not answer every question about insomnia or sleep. The endpoint concerns self-reported total sleep time, not all facets of sleep quality, daytime functioning, or longer-term outcomes. The registry identifies secondary measures at other time points, but those are separate outcomes and do not broaden the primary endpoint’s meaning. A numeric LPS result is not reported in the registry record.

The randomized, double-blind design is relevant to interpreting a comparison between groups, but the registry record does not describe all implementation details, analysis assumptions, missing-data methods, or multiplicity procedures. These limits should accompany interpretation of the p-value and confidence interval. The evidence is specific to the studied participants, the HD-placebo comparison, and the defined Month 1 outcome; it should not be extended automatically to other doses, populations, or outcomes.

In general, statistical significance and clinical importance are different questions. The p-value addresses compatibility with a null comparison under assumptions; the confidence interval describes uncertainty around the estimated group difference. Neither statistic establishes the importance of the change without relevant clinical context and a meaningful-change threshold. Such a threshold is not reported in the registry record.

18. Why This Trial Matters Statistically

This study illustrates why a clinical trial result should be read through its estimand, analysis population, and uncertainty rather than through a p-value alone. The primary measure is a diary-based change in subjective sleep duration, averaged over a specified Month 1 window. That definition makes clear what the estimate addresses and what it does not address: it is not a general measure of every aspect of insomnia or sleep.

The sponsor’s least-squares mean comparison and the simple unadjusted recalculation yield closely aligned point estimates, while representing different analytical approaches. This distinction is important in biostatistics. A calculation from group summaries can serve as a transparent check, but it cannot reproduce a longitudinal model whose full specification is unavailable. The trial’s reported analysis remains the appropriate primary reference.

The record also shows why secondary endpoints and multiplicity need explicit interpretation. Several related measures and assessment periods appear in the outcome record, but adjustment or hierarchy details are not reported. Statistical evidence from secondary comparisons is therefore not equivalent to a single prespecified primary test. Similarly, a rule for calculating an endpoint mean is not a full account of missing-data handling.

Finally, precision and meaning should not be conflated. The primary confidence interval excludes zero under the reported analysis, but the registry record does not give a threshold for clinical importance. Statistical interpretation can describe the estimated difference and its uncertainty while remaining cautious about significance to participants. That separation is central to a clear reading of trial results.

19. Limitations

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

The registry record leaves several trial-specific details unavailable. It does not report the original sample-size justification, allocation ratio, or full statistical analysis plan. Although randomization and double masking are identified, the method of sequence generation, allocation concealment, and masking procedures are not described. These omissions prevent a detailed assessment of design implementation from the registry record alone.

The primary outcome depends on daily electronic diary reports, with Month 1 defined as Days 23-30 and a minimum of 3 days required to calculate the range average. The record does not report adherence to diary completion, the amount or pattern of missing data, or the method used to address missing endpoint values in the sponsor’s longitudinal analysis. It also does not report sensitivity analyses for missing-data assumptions or model diagnostics.

The registry lists multiple outcomes and analyses but does not report a multiplicity strategy or testing hierarchy. This matters particularly for interpreting secondary results. The named LPS secondary outcome lacks a numeric result in the registry record. The record also does not report a clinically important threshold for sTSTm, limiting interpretation of the estimated difference in terms of importance to participants.

Safety information is presented as counts across treatment, follow-up, and additional groups. Death counts are not reported, and the registry entries do not provide formal comparative analyses for the adverse-event summaries. The meaning of the group labels and their relationship across periods is not fully detailed in the posted record. These limitations do not negate the reported estimates, but they restrict how comprehensively the results can be assessed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy Study of Suvorexant in Participants With Primary Insomnia - Study B (MK-4305-029) — NCT01097629.
• Registry record last updated 2019-08-28; status last verified 2019-08.
• Results first posted 2014-09-01.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed Phase III, multicenter, randomized, double-blind, placebo-controlled, parallel-group study in participants with primary insomnia. The primary comparison is suvorexant HD versus placebo for change from baseline in mean subjective total sleep time at Month 1.

The sponsor reports a difference in least-squares means of 26.3 minutes, with a 95% confidence interval from 18.3 to 34.3 and p < 0.001. The posted unadjusted recalculation gives a difference of 26.3 minutes and a 95% confidence interval from 18.31 to 34.29. Secondary results describe related sleep measures at earlier assessment times, while multiplicity handling, fuller missing-data methods, clinical-importance thresholds, and some safety details are not reported in the registry record.