Efficacy of Ramelteon on Speeding Up Sleep in Subjects With Delayed Sleep Phase Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of Ramelteon on Speeding Up Sleep in Subjects With Delayed Sleep Phase Syndrome (NCT00593736), a randomized phase 2 study. The primary outcome is Latency to Persistent Sleep Over a 2-night Average Measured by Polysomnography (Nights 6-7).

2. Clinical Question

3. Trial Design

NCT00593736 was a completed phase 2, randomized, double-blind, placebo-controlled, parallel-group proof-of-concept study sponsored by Takeda. Its official title describes an evaluation of ramelteon to advance sleep timing in individuals with delayed sleep phase syndrome. The brief summary likewise states that the study examined whether once-daily ramelteon could advance sleep timing. The registry record lists enrollment of 132 participants.

Participants were assigned to one of four groups: ramelteon 1 mg once daily, ramelteon 4 mg once daily, ramelteon 8 mg once daily, or placebo once daily. The primary outcome was latency to persistent sleep, assessed as a two-night average by polysomnography on nights 6–7. The primary analysis population was the full analysis set, defined as all randomized participants with at least a baseline assessment and one post-baseline assessment. The arm counts for the primary outcome were 31, 33, 33, and 30, respectively; these are outcome-analysis counts, not a substitute for the registry’s enrollment figure.

The registry record lists a study start of 2007-10 and primary completion of 2008-05, and identifies the study as completed. It also lists secondary sleep outcomes measured over two-night averages, including latency, total sleep time, sleep efficiency, and wake time after sleep onset. Details such as the randomization procedure, allocation ratio, medication schedule beyond once-daily dosing, trial setting, and the original statistical analysis plan are not reported in the registry record. The registry record does not report the original sample-size justification.

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 were screened for 14 days, entered a 7-day placebo run-in, and then were randomized to once-daily (QD) treatment. To enter the double-blind randomization period, subjects must have met the eligible inclusion and none of the exclusion criteria and met sleep diagnostic criteria established during screening polysomnography.

Screening Period and Placebo Run-in

Reasons for not completing this period:

Treatment Period and Placebo Run-out

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was conducted on the full analysis set (FAS), which consisted of all randomized subjects who had at least a baseline assessment and 1 post-baseline assessment.

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 Latency to Persistent Sleep Over a 2-night Average Measured by Polysomnography (Nights 6-7), measured over Nights 6-7.

The primary endpoint was latency to persistent sleep over a two-night average measured by polysomnography on nights 6–7, in minutes. It measures elapsed time from the beginning of the recording to the start of the first 10 minutes of continuous sleep. The registry’s operational definition identifies this as the first 20 consecutive non-wake epochs, with the number of epochs divided by 2.

This endpoint is useful for evaluating how quickly sleep begins after recording starts. A shorter latency corresponds to reaching persistent sleep sooner during the recording. That makes the measure relevant to the study’s interest in sleep timing, but it should not be treated as a direct measurement of a participant’s circadian phase or of the amount by which their sleep schedule shifted. The distinction matters: a change in time to persistent sleep during a recording and a change in the clock timing of sleep are related questions, but they are not identical measurements.

The registry reports least-squares means and standard errors for the primary outcome. The primary population was the full analysis set: randomized participants with at least a baseline assessment and one post-baseline assessment. The registry record does not report further details about how the endpoint was incorporated into the original statistical model or how missing primary measurements were handled.

7. Results Posted in the Registry

• Ramelteon 1 mg QD: mean 59.30 versus 55.12 on control; difference 4.18 (95% CI -14.61 to 22.97), standardized effect d = 0.11; z-test p = 0.663.
• Ramelteon 4 mg QD: mean 39.40 versus 55.12 on control; difference -15.72 (95% CI -34.06 to 2.62), standardized effect d = -0.42; z-test p = 0.093.
• Ramelteon 8 mg QD: mean 55.94 versus 55.12 on control; difference 0.82 (95% CI -17.69 to 19.33), standardized effect d = 0.02; z-test p = 0.931.

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.

Latency to Persistent Sleep Over a 2-night Average Measured by Polysomnography (Nights 13-14)

• 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 1 mg QD: mean 48.36 versus 46.64 on control; difference 1.72 (95% CI -17.45 to 20.89), standardized effect d = 0.05; z-test p = 0.860.
  • Ramelteon 4 mg QD: mean 38.61 versus 46.64 on control; difference -8.03 (95% CI -26.88 to 10.82), standardized effect d = -0.21; z-test p = 0.404.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramelteon 1 mg QD and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramelteon 4 mg QD and the control. The interval gives the range of effects that remain compatible with the data.

Total Sleep Time Over a 2-night Average Measured by Polysomnography (Nights 6-7)

• 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 1 mg QD: mean 376.41 versus 366.23 on control; difference 10.18 (95% CI -12.80 to 33.16), standardized effect d = 0.22; z-test p = 0.385.
  • Ramelteon 4 mg QD: mean 383.51 versus 366.23 on control; difference 17.28 (95% CI -5.32 to 39.88), standardized effect d = 0.38; z-test p = 0.134.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramelteon 1 mg QD and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramelteon 4 mg QD and the control. The interval gives the range of effects that remain compatible with the data.

Total Sleep Time Over a 2-night Average Measured by Polysomnography (Nights 13-14)

• 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 1 mg QD: mean 389.72 versus 388.51 on control; difference 1.21 (95% CI -23.64 to 26.06), standardized effect d = 0.02; z-test p = 0.924.
  • Ramelteon 4 mg QD: mean 378.04 versus 388.51 on control; difference -10.47 (95% CI -35.07 to 14.13), standardized effect d = -0.21; z-test p = 0.404.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramelteon 1 mg QD and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramelteon 4 mg QD and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary sleep measures, covering latency to persistent sleep, total sleep time, sleep efficiency, and wake time after sleep onset. Several are assessed at different night ranges, including nights 6–7 and nights 13–14. These outcomes provide additional views of sleep during the study, but they address distinct features and time points rather than duplicating the primary question exactly.

For the secondary comparisons with numerical estimates available, the recalculated contrasts vary in direction and size, and the intervals include zero. The sponsor-reported ANCOVA p-values listed for those comparisons do not provide a clear pattern of strong evidence across the posted comparisons. This general picture is consistent with the uncertainty in the primary results, but secondary measures cannot resolve the primary endpoint’s limitations or be treated as direct evidence about circadian phase.

Multiplicity is an important consideration because many outcomes and analyses are listed: the registry record reports 60 outcome measures and 180 analyses, with 59 secondary outcomes posted. When many comparisons are made, the chance of finding an apparently unusual result by chance can increase. Unadjusted secondary results therefore generally carry less weight than a prespecified primary analysis, particularly when the registry record does not report a multiplicity strategy. No correction method or hierarchy for the secondary outcomes is reported in the registry record.

The secondary results are best treated as exploratory context. Their interpretation depends on the specific measure, time point, analysis population, and statistical method. The registry record does not report a complete analysis plan explaining how secondary outcomes were prioritized or how missing measurements were handled across them. Individual secondary findings should not be promoted to definitive conclusions without those details and appropriate attention to multiple testing.

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

• Latency to Persistent Sleep Over a 2-night Average Measured by Polysomnography (Nights 13-14)
• Total Sleep Time Over a 2-night Average Measured by Polysomnography (Nights 6-7)
• Total Sleep Time Over a 2-night Average Measured by Polysomnography (Nights 13-14)
• Sleep Efficiency Over a 2-night Average Measured by Polysomnography (0-3 Hours) (Nights 6-7)
• Sleep Efficiency Over a 2-night Average Measured by Polysomnography (0-3 Hours) (Nights 13-14)
• Sleep Efficiency Over a 2-night Average Measured by Polysomnography (0-8 Hours) (Nights 6-7)
• Sleep Efficiency Over a 2-night Average Measured by Polysomnography (0-8 Hours) (Nights 13-14)
• Wake Time After Sleep Onset Over a 2-night Average Measured by Polysomnography (Nights 6-7)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is recorded in minutes, and the registry reports a least-squares mean for each group. A mean describes the group’s average outcome. The reported standard errors describe the precision of those mean estimates, rather than the spread of individual participants’ observations. For example, the primary outcome standard errors range from 6.352 to 6.871 minutes across the four groups.

What does ANCOVA contribute?

The registry identifies ANCOVA as the method used for the sponsor’s reported comparisons. In general, analysis of covariance (ANCOVA) compares group outcomes while adjusting for specified covariates. Adjustment can account for measured features included in the model and may produce estimates different from a simple comparison of group means. The registry record does not report which covariates were included, the model specification, or the adjusted effect estimates. The sponsor’s reported p-values are therefore the available registry results for those analyses; the missing model details limit how fully they can be reconstructed.

How are the recalculated comparisons different?

The recalculated mean differences use the posted arm-level summary statistics to make simple, unadjusted comparisons of each ramelteon group with placebo. They are not ANCOVA results and do not reproduce the sponsor’s adjustment. The recalculated intervals are based on approximate standard deviations derived from the reported standard errors. They provide a transparent, approximate comparison from the posted summaries, but the sponsor’s own ANCOVA analysis takes precedence when the two approaches differ. The discrepancy flag for this trial indicates that the posted sponsor analysis and the simple recalculations should not be treated as interchangeable.

The reported p-values and the recalculated estimates address related but distinct statistical summaries. A p-value describes how compatible the observed data are with a specified null hypothesis under the analysis model; it is not the probability that the null hypothesis is true, nor a measure of the size or importance of an effect. An effect estimate gives a direction and scale, while an interval communicates uncertainty around that estimate. In this record, the adjusted effect estimates for the primary endpoint are not reported, so the sponsor’s ANCOVA p-values cannot be paired with adjusted effect magnitudes from the registry.

Why does the confidence interval matter?

In general, a confidence interval gives a range of values compatible with the data and the method used to construct it. A wide interval signals limited precision: the data do not distinguish closely among a broad range of possible effects. An interval that includes zero for a mean difference is compatible with no difference, as well as with effects in either direction when both signs are within its limits. That does not prove there is no effect. The recalculated primary intervals include zero and span both shorter and longer latencies for each dose versus placebo.

Standard errors are not standard deviations. A standard deviation describes variation among observations, while a standard error describes uncertainty in an estimated mean. The registry reports least-squares means with standard errors, not the raw participant-level observations. That is why the recalculated intervals are approximate rather than a replacement for the sponsor’s modeled comparisons.

In general, over-dispersion matters when data vary more than the statistical model assumes. A model that understates variability can yield standard errors that are too small and intervals that are too narrow; a model that accounts for the variability can produce more realistic uncertainty. The primary outcome is continuous, and the registry record does not report an over-dispersion assessment or any such adjustment. This concept should not be taken to imply that over-dispersion was present in this trial.

The analysis population also affects interpretation. The full analysis set includes randomized participants who had a baseline and at least one post-baseline assessment. It is not described as including every randomized participant regardless of available measurements. The registry record does not explain how specific missing values, withdrawals, or incomplete outcome measurements were treated in the ANCOVA. Without those details, the impact of missing data on the reported comparisons cannot be assessed from the registry record alone.

11. Confidence Intervals and Precision

The recalculated primary mean differences are accompanied by 95% confidence intervals: 4.18 minutes for ramelteon 1 mg versus placebo, with an interval from -14.61 to 22.97; -15.72 minutes for ramelteon 4 mg versus placebo, with an interval from -34.06 to 2.62; and 0.82 minutes for ramelteon 8 mg versus placebo, with an interval from -17.69 to 19.33. These are unadjusted recalculations, not the sponsor’s ANCOVA intervals; the registry does not report the sponsor’s adjusted confidence intervals.

Each recalculated interval includes zero and extends to values on both sides of zero. In general, this means the data are compatible with no mean difference and with differences in either direction across the interval. The intervals are broad relative to the point estimates, particularly for the 1 mg and 8 mg comparisons. The estimates therefore have limited precision: the recalculated summaries do not pin down a narrow range of plausible differences in latency.

A confidence interval is not a guarantee that the true effect lies within its limits, nor does an interval including zero demonstrate equivalence. Equivalence requires a suitable design and a prespecified margin; the registry record does not report an equivalence objective or margin. Likewise, a confidence interval should not be interpreted as the probability that any particular effect value is true.

These intervals come from simple unadjusted calculations based on the posted summary statistics. Since the sponsor used ANCOVA and did not report adjusted effect estimates or intervals in the registry record, the recalculated intervals are best read as a supplemental view of uncertainty, not as the primary inferential result. The sponsor’s own analysis takes precedence.

12. Planning a Similar Trial: Sample Size

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

The planning figures are expressed as participants per arm for 80% power and participants per arm for 90% power. They are not total study enrollment figures and do not describe how many participants were actually enrolled or analyzed. For continuous outcomes such as this primary latency measure, the values represent participants per arm, not total events.

The planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as a reference and considers planning for 100%, 75%, or 50% of that observed effect. The registry record does not report the original trial’s sample-size assumptions or justification; these planning assumptions are for an illustration based on the posted results, not the trial’s original design.

The 80% power column describes a planning target under which a study would have an 80% probability of detecting the specified effect if that effect were present, given the stated assumptions. The 90% power column uses a higher probability target and consequently calls for more participants under the same assumptions. Smaller effects require more participants to detect than larger effects, which is why planning for a smaller fraction of the observed effect raises the required per-arm sample size. When the observed estimate is close to zero, the resulting planning figures can become very large.

These are sample-size planning illustrations, not observed power. Observed power is not a useful substitute for interpreting the estimates and their uncertainty after a trial has been completed. The figures depend on the assumed effect and statistical conditions; they should not be read as evidence that the trial was designed around those assumptions or that the planned effects were clinically important.

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 = 4.180; pooled standard deviation σ = 37.422.
2. n = 2 × (1.96 + 0.842)² × 37.422² / 4.180² = 1,258.1, rounded up to 1,259 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 <- 4.18                      # observed difference in means
sigma <- 37.4215119294337                     # 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(593736)
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 = 1,259 (80% power), 1,685 (90% power)
 75% of observed effect: n per arm = 2,237 (80% power), 2,995 (90% power)
 50% of observed effect: n per arm = 5,033 (80% power), 6,738 (90% power)
power.t.test: 1259.1 
Simulated power at n = 1,259 per arm: 0.795 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparisons as ANCOVA p-values: 0.646 for ramelteon 1 mg versus placebo, 0.084 for ramelteon 4 mg versus placebo, and 0.929 for ramelteon 8 mg versus placebo. The registry does not report adjusted effect estimates or confidence intervals for these comparisons. The sponsor’s analysis is the trial’s reported inferential analysis and takes precedence over the simple recalculations.

The recalculated comparisons use posted least-squares means and standard errors to form unadjusted mean differences and approximate intervals. They do not account for the ANCOVA model or its adjustments. The recalculated p-values are also unadjusted and should not be substituted for the sponsor’s ANCOVA p-values. Differences between the two sets of results are possible because they are based on different analyses; the registry record does not provide enough model detail to reproduce the sponsor’s calculations.

Both sources of results should be interpreted cautiously. The sponsor’s p-values do not report effect magnitude, and the registry record does not include the corresponding adjusted estimates. The recalculated estimates provide a descriptive, approximate view of the arm-level summaries, but are not an alternative adjusted analysis. Neither p-values alone nor the recalculated intervals establish that the groups are equivalent.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 60 outcome measures and 180 analyses, including 59 posted secondary outcomes. Multiple outcomes, time points, doses, and comparisons create a multiplicity issue: the more statistical tests considered, the greater the opportunity for chance findings. In general, a prespecified strategy can address this through methods such as adjustment for multiple comparisons or a hierarchy that prioritizes outcomes. The registry record does not report whether such a strategy was used, how the primary and secondary tests were ordered, or whether the sponsor’s p-values were adjusted. Accordingly, the reported comparisons should not be assumed to account for multiplicity.

The primary analysis population is described as the full analysis set, consisting of randomized participants with at least a baseline assessment and one post-baseline assessment. The record does not report the number excluded from this population, reasons for missing measurements, or the method used to handle missing outcomes. It also does not describe any sensitivity analyses for missing data. The consequences of missingness therefore cannot be evaluated from the registry record alone.

The sponsor identifies ANCOVA for the reported primary comparisons, but the registry record does not report the model covariates, detailed model specification, or adjusted effect estimates. It does not report interim analyses, stopping rules, or the original statistical analysis plan. Those omissions matter because analysis choices can affect estimates, uncertainty, and interpretation.

These gaps do not establish that the trial lacked a statistical plan or multiplicity control; they mean those details are not reported in the registry record. The posted results support interpretation of the named endpoint and comparisons, but they do not allow a full audit of analysis decisions or missing-data assumptions.

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 non-serious adverse event terms

The registry lists zero serious adverse events in each treatment group. The numbers at risk for the serious adverse event reporting are 32 for ramelteon 1 mg, 33 for ramelteon 4 mg, 35 for ramelteon 8 mg, and 32 for placebo. These are the group-specific denominators attached to the serious adverse event results, and they should be kept distinct from the primary outcome analysis counts.

The record also lists other adverse events affecting 7 participants in the ramelteon 1 mg group, 5 in the 4 mg group, 6 in the 8 mg group, and 4 in the placebo group. These are not serious adverse event counts. The registry does not list serious adverse event terms, and death counts are not reported in the registry record.

These figures describe the adverse event information posted for this study; they do not establish the absence of unreported events or provide a comprehensive safety assessment. The group sizes and scope of registry reporting should be considered when interpreting the counts. No medical conclusion about treatment safety follows from these counts alone.

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

The primary results describe latency to persistent sleep during polysomnography on nights 6–7. The sponsor’s ANCOVA p-values are 0.646, 0.084, and 0.929 for the three ramelteon dose comparisons with placebo. The registry does not report the adjusted effect estimates or confidence intervals that would show the magnitude and precision of those modeled comparisons. The unadjusted recalculated estimates have broad intervals that include zero, so they do not precisely determine the direction or size of the group differences.

These findings do not establish equivalence between ramelteon and placebo, nor do they establish a particular degree of change in sleep timing. A non-significant p-value is not proof that two groups have the same outcome. Conversely, the numerical estimate for one group should not be treated as confirmation of a difference when its uncertainty is substantial and the sponsor’s analysis does not provide a reported adjusted effect estimate.

The endpoint measures time from the start of a polysomnography recording to persistent sleep. Although the study’s stated purpose was to evaluate advancing sleep timing, the endpoint is not a direct measure of circadian phase or the clock-time shift in a participant’s sleep schedule. Claims about those distinct outcomes would require measurements and analyses that the registry record does not report.

The appropriate statistical reading is therefore narrow: the posted results offer uncertain comparisons of latency to persistent sleep for the tested doses against placebo, at the stated nights and in the stated analysis population. They do not establish that no effect exists, and they do not by themselves establish a treatment benefit or lack of benefit. Broader interpretation is limited by the missing adjusted estimates, unreported multiplicity strategy, and incomplete reporting of missing-data and analysis-plan details.

18. Why This Trial Matters Statistically

This trial illustrates why the analysis method and the estimand matter in clinical research. A study may describe a broad clinical goal—in this case, advancing the timing of sleep—while its primary endpoint measures a narrower feature: time to persistent sleep after polysomnography begins. Clear distinction between the target question and the operational measure helps prevent overinterpretation.

It also shows why p-values should not stand alone. The registry reports ANCOVA p-values but not the adjusted differences or their confidence intervals. Without those estimates, the sponsor’s results convey limited information about the size and precision of group contrasts. Simple recalculations from summary statistics can add context, but they cannot reproduce an adjusted model when its details and outputs are absent.

The three doses provide several comparisons with placebo, while the record also lists many outcomes and analyses. This makes prespecification and multiplicity handling important to interpretation. The record’s missing information about those choices is a limitation of what can be inferred from its public results, not proof that the underlying trial did not address them.

Finally, planning estimates based on observed effects are not evidence of the trial’s original design rationale. In general, observed effects may be uncertain, and planning around an estimate from a completed study is distinct from designing a future study around a justified target effect. The record provides a useful example of separating descriptive results, modeled inference, and planning illustrations.

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.

Several limitations are specific to the registry information for this trial. The sponsor’s primary ANCOVA results are reported as p-values, but adjusted effect estimates and confidence intervals are not reported in the registry record. The model covariates and other specification details are also absent. This prevents a complete interpretation of the magnitude and precision of the sponsor’s modeled comparisons and limits independent reproduction of those results.

The posted recalculations are unadjusted and use approximate standard deviations derived from reported standard errors. They are not equivalent to the sponsor’s ANCOVA. Because the two approaches differ, the recalculations should be treated as supplemental descriptions; the sponsor’s analysis takes precedence.

The record does not report the original sample-size justification, randomization details, allocation ratio, missing-data methods, interim analyses, or multiplicity strategy. It lists many outcomes and analyses, but does not explain how secondary comparisons were prioritized or adjusted. The full analysis set definition is available, but the record does not detail exclusions from that set or how incomplete measurements were handled.

The primary endpoint is a polysomnographic latency measure, not a direct measure of circadian phase or change in sleep clock time. The distinction is especially relevant because the study’s stated purpose concerns advancing sleep timing. Finally, the serious adverse event counts are posted with group denominators, but death counts are not reported in the registry record. These reporting limitations constrain interpretation and should not be mistaken for evidence that particular procedures or analyses were absent from the conduct of the trial.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy of Ramelteon on Speeding Up Sleep in Subjects With Delayed Sleep Phase Syndrome — NCT00593736.
• Registry record last updated 2012-02-28; status last verified 2012-02.
• Results first posted 2010-03-09.
• 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

NCT00593736 was a completed phase 2 randomized, double-blind, placebo-controlled, parallel-group study of ramelteon in people with delayed sleep phase syndrome. The registry lists 132 enrolled participants assigned to once-daily ramelteon 1 mg, 4 mg, or 8 mg, or placebo. The primary endpoint was latency to persistent sleep, averaged over polysomnography nights 6–7 in the full analysis set.

The registry reports least-squares means and standard errors by group, plus ANCOVA p-values for each dose versus placebo. It does not report adjusted effect estimates or confidence intervals for those sponsor analyses. Unadjusted recalculations show broad intervals that include zero, and should be treated as supplemental rather than as a replacement for the sponsor’s analysis. Serious adverse event counts are zero in all four groups; deaths are not reported in the registry record.

The record does not report the original sample-size justification, multiplicity strategy, or detailed missing-data methods. The posted results support a focused reading of the sleep-latency comparisons, with uncertainty about their magnitude and limited basis for conclusions about sleep timing more broadly.