Facilitation of Zolpidem (≥10 mg) Discontinuation Through Use of Ramelteon in Subjects With Chronic Insomnia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Facilitation of Zolpidem (≥10 mg) Discontinuation Through Use of Ramelteon in Subjects With Chronic Insomnia (NCT00492232), a randomized phase 4 study. The primary outcome is Percentage of Participants Who Discontinued Zolpidem Therapy.

2. Clinical Question

3. Trial Design

The registry describes a randomized, double-blind, placebo-controlled, parallel-group Phase 4 study. The study was completed, with enrollment recorded as 135. The registry lists Takeda as sponsor. The recorded start was 2007-04, and primary completion was 2008-03.

The two groups received ramelteon 8 mg once daily or placebo once daily alongside participants’ current zolpidem therapy. In both groups, zolpidem was to be reduced by dose, frequency, or both, for up to 10 weeks. The primary outcome was assessed at Week 10, after the period in which zolpidem was incrementally reduced from Week 3 to Week 10.

The primary analysis population was narrower than the enrolled population: it comprised randomized participants who took at least one dose of study drug, completed the double-blind treatment period, and had sufficient zolpidem dosage data for the final 7 days. The posted primary arm summaries include 52 participants in the ramelteon group and 49 in the placebo group. The safety summaries use different at-risk counts, so those summaries should not be treated as having the same analysis population as the primary efficacy result.

The registry record does not report the original statistical design assumptions or a detailed account of the randomization procedure, concealment, or blinding assessment. Allocation is listed as randomized and masking as double, but further operational detail is not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Subjects completed a 4-week single-blind placebo run-in period prior to randomization in the double-blind treatment period (DBTP). During this time they took placebo-matching tablets once-daily (QD) with concomitant current zolpidem therapy. Subjects used a daily subject diary to record zolpidem dose reduction, daily activities, and sleep quality.

Placebo Run-in

Reasons for not completing this period:

Double-Blind Treatment

Reasons for not completing this period:

Open-Label Treatment

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was performed on all randomized subjects who took at least 1 dose of study drug, who had completed the DBTP, and who had sufficient zolpidem dosage data in the last 7 days of the DBTP.

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 Percentage of Participants Who Discontinued Zolpidem Therapy, measured over Week 10.

The primary endpoint was the percentage of participants who discontinued zolpidem therapy by Week 10. The registry defines discontinuation as taking no zolpidem during the last 7 days of the double-blind treatment period. The endpoint is therefore a binary outcome for each participant: either the stated discontinuation criterion was met or it was not.

This outcome addresses the study’s stated question about whether ramelteon could facilitate discontinuation while zolpidem was being reduced. It translates the treatment aim into a directly interpretable event rather than measuring only a change in dosage. A participant could have reduced zolpidem without meeting the complete-discontinuation definition, so the endpoint represents a specific threshold of reduction, not every degree of dose change.

The interpretation depends on the recorded assessment window and the defined analysis population. Participants needed to complete the double-blind treatment period and have sufficient dosage data for its final 7 days to be included. The registry does not report further detail about how incomplete endpoint data were handled or how many randomized participants were excluded from this analysis.

7. Results Posted in the Registry

• Ramelteon 8 mg QD: 28.8% (15/52) versus 32.7% (16/49) on control; risk difference -3.8 percentage points (95% CI -21.8 to 14.2), risk ratio 0.88 (0.49–1.59); unadjusted two-proportion z-test p = 0.678.

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.

Change From Baseline in Weekly Zolpidem Dosage During Weeks 1-2

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Ramelteon 8 mg QD: mean -11.80 versus -11.60 on control; difference -0.20 (95% CI -8.75 to 8.35), standardized effect d = -0.01; z-test p = 0.963.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramelteon 8 mg QD and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Weekly Zolpidem Dosage During Weeks 3-4

• 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:
  • Ramelteon 8 mg QD: mean -35.30 versus -35.60 on control; difference 0.30 (95% CI -7.77 to 8.37), standardized effect d = 0.01; z-test p = 0.942.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramelteon 8 mg QD and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Weekly Zolpidem Dosage During Weeks 5-6

• 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:
  • Ramelteon 8 mg QD: mean -40.20 versus -42.10 on control; difference 1.90 (95% CI -6.97 to 10.77), standardized effect d = 0.08; z-test p = 0.675.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramelteon 8 mg QD and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary measures of change in weekly zolpidem dosage across successive study periods, as well as measures of weekly zolpidem frequency. The posted numerical secondary results include dosage changes during Weeks 1-2, Weeks 3-4, and Weeks 5-6. Across those reported periods, the ramelteon and placebo group estimates are close, and the recalculated unadjusted mean-difference intervals include zero. The sponsor’s reported ANCOVA comparisons also do not identify a clear separation between groups in those posted dosage outcomes.

This general pattern is compatible with the primary result, which likewise does not establish a clear between-group difference in complete discontinuation by Week 10. The secondary outcomes are related but not identical: changes in weekly dosage over a time interval do not equal the primary endpoint’s definition of taking no zolpidem in the final 7 days. A participant’s dosage change can therefore inform the course of reduction without establishing complete discontinuation.

Secondary outcomes generally carry less inferential weight when many outcomes or time periods are examined without a reported multiplicity procedure. Repeated testing can increase the chance of obtaining apparently notable findings by chance. The registry record does not report a prespecified hierarchy or adjustment for multiple comparisons, so unadjusted secondary findings should be treated as exploratory rather than as independent confirmation.

The registry record names additional secondary outcomes, including weekly frequency measures, but numerical results for those measures are not reported in the registry record. The record lists 14 outcome measures, 13 analyses, and 13 posted secondary outcomes. It does not explain the relationship among those counts or provide enough information to infer why some measures lack posted numerical results.

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

• Change From Baseline in Weekly Zolpidem Dosage During Weeks 1-2
• Change From Baseline in Weekly Zolpidem Dosage During Weeks 3-4
• Change From Baseline in Weekly Zolpidem Dosage During Weeks 5-6
• Change From Baseline in Weekly Zolpidem Dosage During Weeks 7-8
• Change From Baseline in Weekly Zolpidem Dosage During Weeks 9-10
• Change From Baseline in Weekly Zolpidem Frequency During Weeks 1-2
• Change From Baseline in Weekly Zolpidem Frequency During Weeks 3-4
• Change From Baseline in Weekly Zolpidem Frequency During Weeks 5-6

9. Statistical Interpretation

10. Statistical Methods Explained

What is the primary comparison? The primary outcome is binary, because each participant either met the definition of complete zolpidem discontinuation by Week 10 or did not. The group percentages describe the proportion meeting that definition in each analysis group. The recalculated risk difference compares those proportions by subtracting the placebo proportion from the ramelteon proportion, as a simple unadjusted contrast based on the posted counts.

A risk difference is expressed on the probability scale. A value of zero corresponds to equal event proportions. A negative estimate in the stated direction means that the observed proportion was lower in the ramelteon group than in the placebo group. The estimate is -0.038, and its confidence interval runs from -0.218 to 0.142. Because the interval includes zero, the posted summary data are compatible with no difference as well as with contrasts in either direction.

How do ratios differ from a risk difference? The recalculated risk ratio compares the probability of discontinuation between groups, while the recalculated odds ratio compares the odds of discontinuation. A ratio of one is the null value for either measure. The risk ratio was 0.883 with a 95% confidence interval from 0.491 to 1.588; the odds ratio was 0.836 with a 95% confidence interval from 0.359 to 1.949. Both intervals include one. Risk and odds ratios are not interchangeable with risk differences, and odds ratios can be less intuitive when the outcome is not rare.

What does a confidence interval communicate? A confidence interval describes the uncertainty in an estimate under the statistical method used. It is not a range containing a known fixed proportion of individual participant outcomes, and it does not assign a probability to a particular treatment effect after the data are observed. For this trial, the intervals are broad enough to include the null value and a range of possible effects. Precision is considered further in the interpretation of the posted interval estimates.

What does the p-value add? The unadjusted p-value of 0.678 is a measure of how unusual data at least this discrepant would be under a statistical model in which the groups have no underlying difference, subject to that model’s assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The p-value should be interpreted alongside the effect estimate and its confidence interval, rather than as a stand-alone conclusion.

What is the role of the sponsor’s model? The registry reports logistic regression with an adjusted odds ratio of 0.71, a 95% confidence interval from 0.27 to 1.85, and p = 0.484. An adjusted model can account for covariates included in its specification. The listed analysis description does not identify those covariates, so the adjustment cannot be evaluated further from the registry record. The recalculated comparisons are simple unadjusted summaries, and their estimates need not match an adjusted regression estimate.

How should the secondary continuous outcomes be understood? The posted weekly dosage outcomes are reported as least-squares means with standard errors, and the sponsor’s analyses are described as ANCOVA comparisons of final values. A mean difference expresses a contrast on the dosage scale; its confidence interval conveys uncertainty about that contrast. The registry record also gives recalculated unadjusted comparisons from summary statistics. Such re-calculations are not substitutes for the sponsor’s model, because they do not reproduce its adjustment or participant-level analysis.

The standard error describes the estimated sampling variability of a mean estimate. It is not the spread of individual participants’ dosage changes. Standard errors in the two groups and the reported mean contrasts should be interpreted within the outcome-specific populations and timeframes. The registry record does not describe the full model specification, covariance structure, or missing-data procedure for these analyses.

Why can over-dispersion matter? In general, for count or binary data, a statistical model that assumes less variability than the data actually contain may produce uncertainty estimates that are too small. That can make confidence intervals appear narrower and tests more decisive than warranted. The primary endpoint is binary, but the registry record’s method description does not report a dispersion assessment. No conclusion about over-dispersion can be drawn from that absence.

More broadly, a statistical analysis depends on how outcomes are defined, which participants are included, how missing observations are treated, and which model is used. The registry describes the primary endpoint and its analysis population, and it reports an adjusted logistic regression result. Further analysis details—including covariates and missing-data handling—are not reported in the registry record.

11. Confidence Intervals and Precision

The unadjusted risk-difference estimate for complete zolpidem discontinuation was -0.038, with a 95% confidence interval from -0.218 to 0.142. The interval includes zero, the value corresponding to equal proportions. It also extends on both sides of zero, so the posted summary does not pin down the direction of the underlying group contrast with precision.

The recalculated relative measures are similarly uncertain. The risk ratio was 0.883, with a 95% confidence interval from 0.491 to 1.588; the odds ratio was 0.836, with a 95% confidence interval from 0.359 to 1.949. For both ratios, one is the null value, and both intervals include it. The sponsor’s adjusted odds ratio was 0.71, with a 95% confidence interval from 0.27 to 1.85.

In general, an interval’s width reflects both the amount of information and the variability of the outcome under the analysis. The primary analysis included 52 participants in the ramelteon group and 49 in the placebo group, using the stated completion and endpoint-data requirements. The interval widths indicate that the data do not provide a narrowly determined estimate of the between-group effect. A wide interval does not establish that the true effect is large; it indicates that the estimate is uncertain.

The registry does not report a precision target for the primary outcome or the assumptions used in the trial’s original sample-size design. The statistical planning illustration is a separate calculation based on the observed effect and stated planning assumptions, not a record of the original design rationale.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total participants, for this binary outcome. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for planning is the stated fraction of the observed effect. The original trial’s own design assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the specified effect under those assumptions, if that effect is the true one. The 90% power column gives the corresponding planning estimate for a 90% chance. These are design calculations, not predictions that a study will produce a particular result.

For planning for 100% of the observed effect, the estimates are 2,306 participants per arm for 80% power and 3,086 participants per arm for 90% power. For planning for 75% of the observed effect, they are 4,135 and 5,534 participants per arm. For planning for 50% of the observed effect, they are 9,380 and 12,557 participants per arm. Smaller effects require more participants to detect under the same planning assumptions.

These figures are planning illustrations based on the observed effect, not observed power. They do not describe the size or power of the completed trial and should not be interpreted as evidence about treatment benefit.

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

Worked calculation for this trial

1. Control proportion p₀ = 0.327; treatment proportion p₁ = 0.288; average p̄ = 0.307.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6526 = 1.2791.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6520 = 0.5488.
4. n = (1.2791 + 0.5488)² / (-0.0381)² = 2,305.3, rounded up to 2,306 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.326530612244898                          # control proportion
p1 <- 0.288461538461538                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(492232)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 2,306 (80% power), 3,086 (90% power)
 75% of observed effect: n per arm = 4,135 (80% power), 5,534 (90% power)
 50% of observed effect: n per arm = 9,380 (80% power), 12,557 (90% power)
power.prop.test: 2305.3 
Simulated power at n = 2,306 per arm: 0.799 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison as logistic regression, with an adjusted odds ratio of 0.71, a 95% confidence interval from 0.27 to 1.85, and p = 0.484. The recalculated comparison is an unadjusted analysis of the posted group summaries: its odds ratio is 0.836, with a 95% confidence interval from 0.359 to 1.949 and an unadjusted p-value of 0.678.

These estimates can differ because the sponsor’s result is adjusted and the recalculation is not. The registry record does not specify the covariates used in the adjusted model, so the adjustment cannot be reproduced from the reported summary. The sponsor’s estimate is the registry’s own modeled result; the recalculation is a supplementary, simple summary of the posted counts. The registry record does not flag a discrepancy between the posted results and the recalculation.

Both intervals include the null value for an odds ratio, and neither result provides a precise estimate of the direction or size of the contrast. The sponsor’s result should be read as the reported adjusted analysis, while the unadjusted calculation offers a transparent comparison based on the group-level data. Neither should be interpreted without its interval and analysis population.

15. Multiplicity, Missing Data and Analysis Populations

Several outcomes and time periods are listed, including changes in weekly dosage and frequency. The registry record does not report whether the primary endpoint was designated within a formal testing hierarchy, whether secondary outcomes were confirmatory or exploratory, or whether any multiplicity adjustment was planned or applied. Without that information, the family of hypotheses used for formal inference cannot be reconstructed from the record.

When multiple outcomes are tested, the chance of at least one apparently unusual result can increase if each is judged separately without adjustment. This general concern is one reason unadjusted secondary findings warrant caution. It does not change the numerical endpoint estimates, but it affects how much inferential weight can be placed on a collection of separate p-values. The registry lists 14 outcome measures, 13 analyses, and 13 posted secondary outcomes; further explanation of those totals is not reported in the registry record.

The primary analysis population is defined as randomized participants who took at least one dose of study drug, completed the double-blind treatment period, and had sufficient zolpidem dosage data in the last 7 days. This is not described as an analysis of every randomized participant regardless of completion or available data. The number and reasons for exclusions from the primary analysis, and the handling of missing outcome data, are not reported in the registry record.

The registry record also does not report whether missing observations were imputed, whether sensitivity analyses were conducted, or whether alternative analysis populations were examined. These details matter because conclusions from a completer-and-data-available population can depend on how participants with incomplete follow-up differ from those included. No direction or magnitude of such a potential effect can be inferred from the information reported.

Other details that would help assess the analysis—including the adjusted model covariates, the complete statistical analysis plan, and interim-analysis procedures—are not reported in the registry record. Their absence limits independent assessment of the planned inferential framework; it does not by itself show that a particular method was or was not used.

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: coronary artery disease (1.4%).

The serious adverse event summaries list 0 events among 64 participants at risk in the ramelteon group and 1 event among 70 participants at risk in the placebo group. These are descriptive counts over the safety population recorded for those summaries. The at-risk counts differ from the primary efficacy-analysis counts, so the safety and primary endpoint figures refer to different reported populations.

The registry lists coronary artery disease at 1.4% among the top serious adverse event terms. The record does not provide an arm attribution for that term in the information reported, so it should not be assigned to either group from these figures alone. Death counts are not reported in the registry record.

Other adverse events were recorded for 11 of 64 participants at risk in the ramelteon group and 7 of 70 in the placebo group. These totals are not the same as serious adverse event counts. The registry summaries are descriptive and do not establish a comparative safety effect; they do not provide event-level context, duration, severity detail, or an adjusted comparison in the record.

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

The primary result describes the proportion of participants meeting a specific definition of zolpidem discontinuation at Week 10: no zolpidem during the final 7 days of the double-blind treatment period. In the analyzed groups, the posted percentages were 28.8% with ramelteon and 32.7% with placebo. The unadjusted risk-difference interval includes no difference and spans possible contrasts in either direction.

These findings do not establish that ramelteon improved discontinuation, nor do they establish that the treatments are equivalent. The estimates are uncertain, and the analysis includes participants who completed the treatment period and had sufficient dosage data. The record does not report the missing-data analyses needed to assess how the result might change under other assumptions about participants without complete endpoint information.

The endpoint also has a defined scope. It concerns complete discontinuation by a particular time point, not every possible reduction in zolpidem dosage, the durability of discontinuation after the treatment period, or other aspects of insomnia. Secondary dosage measures cover some earlier periods, but they do not replace the primary definition. Follow-up beyond the treatment period is not reported in the registry record.

The trial was randomized, double-blind, placebo-controlled, and parallel-group, which describes its design, but the result still depends on the analysis population, outcome definition, precision, and reporting detail. The posted data support a cautious statistical description of the measured comparison. They do not by themselves answer questions outside that outcome and study period.

18. Why This Trial Matters Statistically

This trial illustrates why an endpoint’s operational definition matters. Complete discontinuation was not defined as any reduction in zolpidem; it required no use during the final 7 days of the double-blind treatment period. That distinction separates an all-or-none endpoint from the secondary measures of dosage change over specified periods.

It also demonstrates the value of presenting an effect estimate with its uncertainty. The group percentages alone may look like a straightforward comparison, but the risk-difference confidence interval includes zero and extends in both directions. The result is not simply a binary verdict based on a p-value; its precision determines how strongly the data constrain plausible effects.

The registry includes both an adjusted sponsor analysis and enough group-level information for an unadjusted recalculation. The two approaches answer related but not identical statistical questions. Comparing them helps distinguish model-based adjustment from a transparent summary of observed group counts, while also showing why the analysis specification matters.

Finally, the outcome and safety populations differ, and the primary analysis requires treatment completion and adequate endpoint data. These features make analysis-population definitions and missing-data reporting important for interpretation. The record’s absence of detail on multiplicity and some analysis procedures limits how fully the inferential plan can be assessed. Those are statistical reporting considerations, not evidence for a particular treatment conclusion.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary analysis is limited to randomized participants who took at least one dose, completed the double-blind treatment period, and had sufficient dosage data in the final 7 days. The registry does not report the number or characteristics of participants excluded under these criteria, or how missing endpoint data were handled. The reported percentages therefore should not be read as outcomes for everyone enrolled.

The unadjusted recalculation uses posted group summaries and cannot reproduce the sponsor’s adjusted logistic regression. The adjustment variables are not reported in the registry record. The record also does not provide a detailed statistical analysis plan, original sample-size rationale, interim-analysis information, or a reported multiplicity procedure. These omissions limit assessment of prespecification and model choices.

The primary endpoint is tied to Week 10 and a final-7-day definition. The registry record does not report whether discontinuation was sustained after that point. Weekly dosage and frequency measures could provide complementary information, but numerical results are not available for all named outcomes in the record.

Safety summaries use at-risk counts different from those for the primary analysis, and the reported serious-event term is not linked to a group in the available summary. Death counts are not reported in the registry record. These descriptive safety data do not provide a complete account of event timing, severity, or comparative risk.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Facilitation of Zolpidem (≥10 mg) Discontinuation Through Use of Ramelteon in Subjects With Chronic Insomnia — NCT00492232.
• Registry record last updated 2010-07-20; status last verified 2010-07.
• Results first posted 2009-07-17.
• 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 describes a completed, randomized, double-blind, placebo-controlled, parallel-group Phase 4 study of ramelteon 8 mg once daily versus placebo during reduction of current zolpidem therapy in participants with chronic insomnia. Enrollment was recorded as 135; the study start was 2007-04 and primary completion was 2008-03.

The primary outcome was complete zolpidem discontinuation by Week 10, defined as no zolpidem use in the final 7 days of the double-blind treatment period. The posted percentages were 28.8% for ramelteon and 32.7% for placebo. The unadjusted risk difference was -0.038, with a 95% confidence interval from -0.218 to 0.142. The sponsor reported an adjusted odds ratio of 0.71, with a 95% confidence interval from 0.27 to 1.85.

The registry also lists dosage and frequency outcomes and descriptive safety summaries. Further details on missing-data handling, multiplicity, model covariates, and the original design assumptions are not reported in the registry record.