Efficacy and Safety of Ramelteon Sublingual as Adjunctive Therapy for Maintenance Treatment of Bipolar I Disorder: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Ramelteon Sublingual as Adjunctive Therapy for Maintenance Treatment of Bipolar I Disorder (NCT01467713), a randomized phase 3 study. The primary outcome is Time From Randomization to Any Relapse.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, double-blind, placebo-controlled, parallel-group study sponsored by Takeda. The official title describes once-daily TAK-375SL as adjunctive therapy to treatment as usual for maintenance treatment of Bipolar I disorder in adults. The registry identifies four groups: matching placebo and sublingual ramelteon at 0.1 mg, 0.4 mg, or 0.8 mg, each taken nightly at bedtime. Arm descriptions state that treatment could continue for up to 9 months.

The registry reports enrollment of 642. The primary endpoint timeframe is described as randomization to Month 12 of the double-blind treatment period. That timeframe and the arm descriptions’ treatment duration of up to 9 months are both recorded; an explanation of how they relate is not reported in the registry record. The study started in 2011-12, and primary completion is recorded as 2015-03. Its status is terminated. The reason for termination is not reported in the registry record.

The primary analysis population was not simply everyone enrolled: it included randomized participants who received at least 1 dose and had at least one valid post-baseline primary efficacy value. Participants without relapse were censored. Arm-level primary outcome summaries list 157.0 participants for placebo, 162.0 for 0.1 mg, 154.0 for 0.4 mg, and 149.0 for 0.8 mg. These analysis counts do not describe all details of participant flow, which are not reported in the registry record. The original design’s allocation ratio, sample-size justification, and planned statistical procedures are 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: Participants with a diagnosis of bipolar disorder were enrolled equally in 1 of 4 treatment groups, once a day placebo, Tak-375 SL (ramelteon) 0.1 mg, 0.4 mg or 0.8 mg.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set included all randomized participants who received at least 1 dose of study drug and had at least one valid post-baseline value for assessment of primary efficacy. Participants without relapse were censored.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Time From Randomization to Any Relapse, measured over Randomization to Month 12 double-blind treatment period.

The primary endpoint was time from randomization to any relapse, measured in days over the double-blind treatment period through Month 12. Relapse could be determined by the Principal Investigator or by criteria specified in the registry: depression with a MADRS score of at least 16; mania or hypomania with a YMRS total score of at least 14; a mixed episode meeting the listed MADRS and YMRS thresholds; psychiatric hospitalization for bipolar disorder; electroconvulsive therapy; or a psychotropic medication change prescribed for treatment of depression, mania, hypomania, or mixed episodes.

Time-to-relapse endpoints are useful when the timing of an event matters, rather than only whether it occurred by a particular assessment. Participants who had not relapsed were censored in the stated primary analysis population. In general, censoring allows a participant’s observed follow-up to contribute information up to the point at which the outcome is no longer observed, without treating that participant as having relapsed at that time.

The registry also presents an arm-level mean and standard error for the primary outcome. Those descriptive summaries are not the same as a time-to-event comparison that accounts for event timing and censoring. The registry’s reported Log Rank analyses express comparisons as hazard ratios. The analysis population definition and the breadth of qualifying relapse events are important context for interpreting both kinds of summaries.

7. Results Posted in the Registry

• Ramelteon SL 0.1 mg: mean 287.70 versus 248.30 on control; difference 39.40 (95% CI 15.90 to 62.90), standardized effect d = 0.37; z-test p = 0.001.
• Ramelteon SL 0.4 mg: mean 253.10 versus 248.30 on control; difference 4.80 (95% CI -16.88 to 26.48), standardized effect d = 0.05; z-test p = 0.664.
• Ramelteon SL 0.8 mg: mean 223.90 versus 248.30 on control; difference -24.40 (95% CI -46.18 to -2.62), standardized effect d = -0.25; z-test p = 0.028.

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.

Time From Randomization to Relapse Due to Depression

• 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 SL 0.1 mg: mean 242.10 versus 256.50 on control; difference -14.40 (95% CI -33.01 to 4.21), standardized effect d = -0.17; z-test p = 0.129.
  • Ramelteon SL 0.4 mg: mean 260.80 versus 256.50 on control; difference 4.30 (95% CI -16.14 to 24.74), standardized effect d = 0.05; z-test p = 0.680.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramelteon SL 0.1 mg 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 SL 0.4 mg and the control. The interval gives the range of effects that remain compatible with the data.

Time From Randomization to Relapse Due to Mania/Hypomania or Mixed Episode

• 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 SL 0.1 mg: mean 319.30 versus 150.20 on control; difference 169.10 (95% CI 156.80 to 181.40), standardized effect d = 2.98; z-test p = <0.001.
  • Ramelteon SL 0.4 mg: mean 269.50 versus 150.20 on control; difference 119.30 (95% CI 111.42 to 127.18), standardized effect d = 3.39; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Ramelteon SL 0.1 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Ramelteon SL 0.4 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time From Randomization to Relapse Due to Depression From PI Judgement and/or MADRS ≥16

• 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 SL 0.1 mg: mean 245.10 versus 265.00 on control; difference -19.90 (95% CI -37.24 to -2.56), standardized effect d = -0.25; z-test p = 0.024.
  • Ramelteon SL 0.4 mg: mean 262.50 versus 265.00 on control; difference -2.50 (95% CI -21.96 to 16.96), standardized effect d = -0.03; z-test p = 0.801.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Ramelteon SL 0.1 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ramelteon SL 0.4 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry names a range of secondary questions, including relapse due to depression, mania or hypomania, mixed episodes, hospitalization, electroconvulsive therapy, and psychotropic medication changes. The numerical summaries available for several of these outcomes do not form a uniform pattern across doses and outcomes. Some recalculated contrasts favor a longer mean time in one group, while others point in the opposite direction or are close to no mean separation. This variation does not establish a consistent effect across relapse types.

These secondary summaries relate to the primary result by examining narrower or related event definitions, but they do not replace the primary composite time-to-relapse analysis. In general, component outcomes may help describe which events contribute to a broad endpoint, but comparisons can become less stable when event counts are limited. The registry does not report a multiplicity strategy for the secondary analyses. Without such a plan, unadjusted secondary p-values carry less weight because examining many outcomes creates more opportunities for apparently notable results to occur by chance.

For the secondary outcomes with numerical summaries, the recalculated comparisons are mean-based and unadjusted. They should therefore be distinguished from sponsor-reported time-to-event analyses. The registry lists additional secondary outcome definitions, but numerical results for the other named outcomes are not reported in the registry record. No overall claim about a secondary-outcome pattern can be based on the available subset alone. These results are best treated as exploratory context rather than independent confirmation of the primary result.

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

• Time From Randomization to Relapse Due to Depression
• Time From Randomization to Relapse Due to Mania/Hypomania or Mixed Episode
• Time From Randomization to Relapse Due to Depression From PI Judgement and/or MADRS ≥16
• Time From Randomization to Relapse Due to Mania/Hypomania
• Time From Randomization to Relapse Due to Mixed Episode
• Time From Randomization to Relapse Due to Psychiatric Hospitalization for Bipolar Disorder
• Time From Randomization to Relapse Due to Electroconvulsive Therapy (ECT) Administration
• Time From Randomization to Relapse Due to Psychotropic Medication Change Prescribed for the Treatment of Depression, Mania/Hypomania or Mixed Episodes

9. Statistical Interpretation

10. Statistical Methods Explained

What does a hazard ratio describe?

The sponsor’s primary results use Log Rank analyses and report hazard ratios. In general, a hazard ratio compares the event rates over time between groups, conditional on participants remaining under observation and not yet having experienced the event. A hazard ratio below 1 is directionally consistent with a lower event hazard in the ramelteon group than in placebo; a value above 1 is directionally consistent with a higher hazard. This directional description does not establish a treatment effect. The uncertainty interval and the analysis design also matter.

For 0.1 mg, the first listed hazard ratio is 0.77; for 0.4 mg it is 0.78; and for 0.8 mg it is 1.06. The corresponding 98.3% confidence intervals all include 1. The registry gives a second set of estimates for these comparisons as well, and those intervals also include 1. The record does not explain why both sets are listed or identify a distinction between them. The repeated p-values do not resolve that uncertainty.

Why do censoring and event timing matter?

In general, a time-to-event analysis uses information about when an event occurs, not just a group average or a count at one moment. Participants whose relapse has not occurred by the end of their observed follow-up are censored, as described for the primary population. Censoring is not the same as observing that a relapse never occurred. The length and pattern of follow-up, and how censoring is handled, can affect the information available to the analysis. Details such as the number censored, reasons for censoring, and handling of missing follow-up are not reported in the registry record.

The endpoint also includes several pathways to an event: clinical rating thresholds, investigator determination, hospitalization, electroconvulsive therapy, or medication changes for specified episode types. In general, a composite endpoint can capture more than one type of clinically relevant event, but its overall result does not by itself show which component contributed most. The registry lists related secondary endpoints, but component-level event counts for the primary composite are not reported in the registry record.

What does the mean-based recalculation do?

The arm summaries report a mean and standard error in days. The recalculated comparisons use those posted summary statistics to form unadjusted mean differences and confidence intervals. A mean difference describes the separation between two group means on the days scale. In general, a confidence interval around a mean difference reflects uncertainty under the assumptions of that calculation. It is not the same quantity as a hazard ratio and does not preserve all the information about event times and censoring.

The recalculated primary comparisons are 39.4 days for 0.1 mg versus placebo, 4.8 days for 0.4 mg, and -24.4 days for 0.8 mg. Their intervals and unadjusted p-values do not match the interpretation conveyed by the sponsor’s reported Log Rank results. The registry record identifies a discrepancy, so the sponsor’s own analysis takes precedence. The recalculation is useful as a transparent comparison of posted summaries, but it should not be treated as a replacement primary analysis or as a resolution of the discrepancy.

How should standard errors, confidence intervals, and p-values be read?

In general, a standard error describes the sampling uncertainty in an estimate; it is not the spread of individual participant outcomes. A confidence interval gives a range of values compatible with the estimate under the method’s assumptions and stated confidence level. Wider intervals indicate less precision than narrower intervals. The sponsor reports 98.3% confidence intervals for the hazard ratios, while the recalculated mean differences have intervals reported in the comparison results. These intervals arise from different estimands and methods, so they should not be compared as if they were measuring precisely the same quantity.

A p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. The registry’s multiplicity strategy and detailed statistical analysis plan are not reported in the registry record. Consequently, the listed p-values should be interpreted as reported rather than assumed to have a particular adjustment for multiple comparisons.

Why can over-dispersion matter in other settings?

In general, over-dispersion occurs when observed variability is greater than a statistical model expects. It can make standard errors too small if the model fails to account for the extra variation, which can make intervals too narrow and tests too optimistic. This is a general statistical consideration, not a reported feature of this trial. The registry’s primary analyses are time-to-event analyses, and over-dispersion is not identified as an issue in the registry record. The methods used for any adjustment to account for variation beyond model assumptions are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor’s confidence intervals are wide relative to their point estimates. For the first reported Log Rank analysis, the 0.1 mg hazard ratio is 0.77 with a 98.3% confidence interval from 0.42 to 1.39; the 0.4 mg estimate is 0.78 with an interval from 0.43 to 1.43; and the 0.8 mg estimate is 1.06 with an interval from 0.60 to 1.86. Each range includes 1. In general, a confidence interval that includes 1 for a hazard ratio does not rule out no relative hazard difference, and its breadth indicates that the estimate is not highly precise.

The second listed set of sponsor estimates is also imprecise: its confidence intervals extend from 0.48 to 1.61 for 0.1 mg, from 0.42 to 1.49 for 0.4 mg, and from 0.60 to 1.95 for 0.8 mg. The registry does not explain the distinction between the two sets, so their precision should not be used to infer a difference in analysis populations or methods.

The recalculated mean-difference intervals likewise vary in what they include. The interval for 0.1 mg is 15.9 to 62.9 days; for 0.4 mg it is -16.88 to 26.48 days; and for 0.8 mg it is -46.18 to -2.616 days. These intervals describe the recalculated mean contrasts, not the sponsor’s time-to-event estimates. The discrepancy between them is an important limitation on interpretation. In general, intervals express uncertainty under their analysis assumptions; they do not account for unreported sources of bias, missing data, or multiplicity decisions.

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 illustrations based on the observed effect, not a reconstruction of the trial’s original design. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each comparison, the illustration considers the full observed effect and smaller effects described as 75% and 50% of that observed effect. Smaller effects require more participants to detect, all else equal.

For these mean-difference comparisons, the reported planning figures are participants per arm. In general, 80% power means that a study of the stated size would have an 80% chance of detecting the specified effect at the stated significance level if the assumptions and effect were correct. The 90% power column expresses a higher chance under those same assumptions and therefore generally requires more participants. These are planning interpretations, not findings about the participants who took part. This is not observed power.

The distinction between participants and events matters: the stated convention is that time-to-event planning tables give the total number of events, using the Schoenfeld method, while all other planning tables give participants per arm. Here, the displayed planning illustrations are based on mean differences and therefore use participants per arm. Their large variation across comparisons reflects the different observed effect sizes used in each calculation. The original trial’s sample-size assumptions and justification are not reported in the registry record, so these illustrations do not establish what the investigators planned or expected before the study.

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 = 39.400; pooled standard deviation σ = 107.223.
2. n = 2 × (1.96 + 0.842)² × 107.223² / 39.400² = 116.3, rounded up to 117 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 <- 39.4                      # observed difference in means
sigma <- 107.222977712461                     # 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(1467713)
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 = 117 (80% power), 156 (90% power)
 75% of observed effect: n per arm = 207 (80% power), 277 (90% power)
 50% of observed effect: n per arm = 466 (80% power), 623 (90% power)
power.t.test: 117.2 
Simulated power at n = 117 per arm: 0.802 (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’s own primary analyses are the Log Rank comparisons reported as hazard ratios with 98.3% confidence intervals and p-values. The registry also contains simple recalculations of mean differences based on the posted arm summaries. Those calculations use a different summary and analytic approach from the reported time-to-event method, and their estimates and p-values differ from the sponsor’s results.

The registry marks a discrepancy between these analyses. In that circumstance, the sponsor’s own analysis takes precedence; the recalculated results should be treated as descriptive, unadjusted comparisons rather than as a correction to the sponsor’s analysis. They do not explain why the sponsor results differ, and they do not resolve which set of the two listed sponsor Log Rank results should be emphasized. The reason for the two sponsor result sets is not reported in the registry record.

The sponsor’s reported intervals include 1 for every dose comparison in both listed sets. That uncertainty should remain central when reading the results. The registry’s statistical analysis plan, including any planned hierarchy or multiplicity adjustment, is not reported in the registry record. Accordingly, the reported sponsor results are the primary reference for interpreting the endpoint, while the mean-based recalculations are a limited secondary check on the posted summaries.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 11 outcome measures and 6 analyses, and it names multiple primary and secondary comparisons. Testing several doses against placebo and examining several related relapse outcomes raises a general multiplicity concern: when many hypotheses are tested, the chance of at least one apparently unusual result can increase. Statistical approaches can control or describe that concern through a prespecified hierarchy, adjustment, or other plan. The multiplicity approach for this trial is not reported in the registry record.

The p-values attached to the recalculated mean differences are explicitly unadjusted. They should not be interpreted as if a correction for all dose and outcome comparisons had been applied. The sponsor’s p-values are reported, but whether they are adjusted and how they relate to a planned testing hierarchy are not reported in the registry record. The two sets of sponsor results also lack an explanation in the record. These gaps limit how confidently any single p-value can be interpreted as confirmatory.

The primary analysis population is described: randomized participants who received at least 1 dose and had at least one valid post-baseline primary efficacy value, with participants without relapse censored. Further details on missing data, censoring patterns, reasons for discontinuation, sensitivity analyses, and any imputation procedures are not reported in the registry record. The handling of missing values can affect estimates when participants with incomplete follow-up differ from those with complete observation. In general, transparent reporting of these choices helps readers assess whether results depend on assumptions about unobserved outcomes.

The original statistical analysis plan, including the prespecified primary analysis, sample-size justification, interim analyses, and any analysis-population distinctions beyond the stated definition, is not reported in the registry record. These omissions do not show that a particular procedure was or was not used; they mean that the registry record does not establish it. Interpretation should therefore distinguish the methods explicitly reported from details that remain unavailable.

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: bipolar i disorder (1.2%), suicidal ideation (1.2%), bipolar disorder (0.6%), aggression (0.6%), suicide attempt (0.6%).

Serious adverse events were reported for groups with 163 participants at risk in the placebo group, 164 in the 0.1 mg group, 159 in the 0.4 mg group, and 154 in the 0.8 mg group. The corresponding numbers affected by a serious adverse event were 10, 14, 6, and 8. These denominators differ from the arm counts in the primary efficacy summaries, so the safety and efficacy figures should not be treated as if they came from identical analysis populations.

The registry lists serious adverse event terms including Bipolar I disorder and suicidal ideation at 1.2% each, and bipolar disorder, aggression, suicide attempt, and depression at 0.6% each. These term percentages are not presented by treatment arm in the available record, so they do not identify which group contributed the events. The counts and terms describe reported events; they do not alone establish that a study drug caused an event or permit a comparative safety conclusion.

Death counts are not reported in the registry record. Exposure duration by group, event timing, and detailed event-level descriptions are also not reported in the registry record. Those limits matter when comparing safety summaries across groups or considering how long participants were observed.

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

The registry record describes a randomized, masked comparison of three sublingual ramelteon doses with matching placebo as adjunctive treatment for adults with Bipolar I disorder. Its primary question concerns the timing of a broad relapse endpoint, and the sponsor’s own reported analyses use Log Rank hazard ratios. In both sets of reported sponsor comparisons, the confidence intervals include 1, and the listed p-values do not indicate a clearly resolved difference under those analyses.

That statement is about the uncertainty in the posted estimates; it is not proof that the groups are identical. The confidence intervals allow a range of possible relative hazards, and their breadth limits precision. The mean-based recalculations give different estimates and p-values, but they are unadjusted calculations from summaries and do not replace the sponsor’s time-to-event analysis. Because the registry identifies a discrepancy, the sponsor’s own analysis takes precedence.

The endpoint combines several definitions of relapse and related clinical events. As a result, an overall primary comparison does not identify which component drives the result. The secondary summaries offer some additional context but are mixed, unadjusted, and not accompanied by a reported multiplicity plan. They cannot independently settle the primary question.

These results do not, on their own, establish whether ramelteon is beneficial or harmful, whether any dose is preferable, or how findings apply outside the enrolled study population. Such conclusions would require careful consideration of the complete study report, the analysis plan, participant flow, follow-up, and safety information. The registry record does not report several of those details, including the reason the study was terminated.

18. Why This Trial Matters Statistically

This trial illustrates why the statistical scale and analysis method matter. The primary question is about time until relapse, and the sponsor reports hazard ratios from Log Rank analyses. The registry also provides arm means and standard errors, from which unadjusted mean differences can be recalculated. Those summaries lead to a different pattern from the sponsor’s time-to-event results. A simple mean comparison and a time-to-event analysis do not necessarily answer the same question, particularly when participants can be censored.

The record also shows why uncertainty intervals deserve attention alongside point estimates and p-values. The sponsor’s reported confidence intervals include 1 across dose comparisons, and the duplicate sets of sponsor estimates are not explained. An estimate alone can seem more definite than the data warrant; the interval shows the range of relative hazards compatible with the reported analysis.

Multiplicity is another central issue in a trial with several doses and related relapse outcomes. Secondary results can inform questions about endpoint components, but unadjusted analyses across many outcomes are less compelling as confirmatory evidence. The record does not state how multiplicity was handled.

Finally, the planning illustrations should not be mistaken for the trial’s original design or for evidence about its observed power. They show how sample-size requirements change under stated hypothetical effects and assumptions. Together, these features make the study a useful example of separating sponsor-reported inference, descriptive summaries, exploratory secondary findings, and assumptions that the registry does not document.

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 specific to this trial affect interpretation. The study status is terminated, but the reason for termination is not reported in the registry record. The registry gives enrollment and arm-level efficacy counts, but a detailed participant flow, including withdrawals, follow-up duration by group, and numbers censored, is not reported in the registry record. Those details would help readers understand how much outcome information contributed to the time-to-event analysis.

The record lists two sets of sponsor Log Rank estimates for the same dose comparisons without explaining their distinction. It also contains recalculated mean differences that diverge from the sponsor’s time-to-event results. The sponsor’s own analysis takes precedence, but the source of the discrepancy and the relationship between the two sponsor result sets are not reported in the registry record.

The primary outcome is composite, combining clinical rating thresholds, investigator judgment, hospitalization, electroconvulsive therapy, and medication changes. Component-specific contribution to the primary result is not reported in the registry record. Secondary outcomes are numerous, and the multiplicity strategy is not reported. The available secondary summaries are unadjusted mean comparisons rather than a complete set of sponsor-reported time-to-event analyses.

The registry does not report the original sample-size justification, prespecified statistical analysis plan, interim analyses, missing-data methods, or sensitivity analyses. Arm descriptions specify treatment for up to 9 months while the primary timeframe extends to Month 12; how these durations relate is not reported in the registry record. Serious adverse event counts are available, but the listed serious terms are not broken down by treatment group in the available record, and death counts are not reported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Ramelteon Sublingual as Adjunctive Therapy for Maintenance Treatment of Bipolar I Disorder — NCT01467713.
• Registry record last updated 2016-05-16; status last verified 2016-04.
• Results first posted 2016-05-16.
• 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

NCT01467713 is a randomized, double-blind, placebo-controlled, quadruple-masked, parallel-group Phase 3 study sponsored by Takeda. It evaluated sublingual ramelteon at 0.1 mg, 0.4 mg, and 0.8 mg as adjunctive therapy to treatment as usual for maintenance treatment of Bipolar I disorder in adults. Enrollment was 642, the study started in 2011-12, primary completion was 2015-03, and status is terminated.

The primary endpoint was time from randomization to any relapse over the double-blind period through Month 12. Sponsor-reported Log Rank hazard-ratio confidence intervals include 1 for all three dose comparisons in both listed result sets. Recalculated mean differences differ from the sponsor analysis; the sponsor’s own analysis takes precedence. The record does not explain the duplicate sponsor results, the termination, or several key statistical and missing-data procedures.