Uptitration Trial of Flibanserin Versus Placebo in Premenopausal Women With Hypoactive Sexual Desire Disorder: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Uptitration Trial of Flibanserin Versus Placebo in Premenopausal Women With Hypoactive Sexual Desire Disorder (NCT00360555), a randomized phase 3 study. The primary outcome is Change From Baseline in the Frequency of Satisfying Sexual Events (SSE) as Recorded in the eDiary..

2. Clinical Question

3. Trial Design

This was a phase 3 randomized, double-masked, parallel-group trial. The registry reports enrollment of 1584 and marks the study completed. The listed start was 2006-07, and primary completion was 2008-03. A separate overall completion date is not reported in the registry record.

The study evaluated flibanserin for premenopausal women with hypoactive sexual desire disorder, with efficacy assessed against a parallel placebo group. The four registry arms were Flibanserin 25 mg b.i.d, Flibanserin 50mg Qhs/b.i.d, Flibanserin 50mg b.i.d./100mg Qhs, and Placebo. The official title describes the regimens as 25 mg twice daily, 50 mg twice daily, and 100 mg in the evening, while the detailed arm labels include bedtime and combined dose wording. The exact sequence and timing of dose changes are not reported in the registry record, so the labels should not be treated as a complete dosing protocol.

The primary efficacy outcome used the Full Analysis Set. This included participants who received at least one post-dose, on-treatment efficacy assessment. The registry states that efficacy endpoints were analyzed primarily using this population. It does not report the number contributing to each analysis beyond the arm-level counts posted with the endpoint results. Randomization and double masking describe key design safeguards, but the method of sequence generation, concealment procedures, and details of masking are not reported in the registry record.

The registry lists two outcome measures, but it posts no secondary outcome results. It also contains no analysis entries. The original sample-size rationale, the trial’s prespecified statistical analysis plan, and any planned interim analyses are not reported in the registry record. Those omissions limit how fully the design can be reconstructed from the posted information alone.

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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Participants who received at least one post-dose on-treatment efficacy assessment were included in the Full Analysis Set (FAS). Efficacy endpoints were analyzed primarily using the FAS.

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: Demographic data are available for participants who were included in the "treated" analysis population of 1,581 participants.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in the Frequency of Satisfying Sexual Events (SSE) as Recorded in the eDiary., measured over baseline to 28 weeks.

The primary endpoint was change from baseline in the frequency of satisfying sexual events, recorded in an electronic diary and expressed as satisfying sexual events (SSEs) per 28 days. The reported timeframe was baseline to 28 weeks. For each arm, the posted result is a mean change with a standard deviation; the registry identifies the endpoint parameter as a mean and the dispersion measure as a standard deviation.

The diary-based monthly measure was constructed by scaling the recorded events to a 28-day period: the registry describes total monthly events as 28 multiplied by the sum of events and divided by the sum of days entered. This approach expresses diary entries on a common monthly time basis when the number of days entered may vary. It is the registry’s stated calculation for eDiary endpoints, rather than an independent re-analysis of diary records.

Using change from baseline focuses the comparison on how the recorded frequency changed over the stated follow-up, rather than only on the endpoint value. A mean summarizes the average change in each arm, while the standard deviation describes the spread of individual changes around that mean. The endpoint therefore communicates both an average group-level result and variability among participants. It does not, by itself, show the distribution of individual responses or explain why diary entries may be missing. The registry does not report the diary completion pattern or the handling of incomplete entries in enough detail to assess those aspects.

7. Results Posted in the Registry

• Flibanserin 25 mg b.i.d: mean 1.40 versus 1.10 on control; difference 0.30 (95% CI -0.19 to 0.79), standardized effect d = 0.09; z-test p = 0.232.
• Flibanserin 50mg Qhs/b.i.d: mean 1.40 versus 1.10 on control; difference 0.30 (95% CI -0.19 to 0.79), standardized effect d = 0.09; z-test p = 0.227.
• Flibanserin 50mg b.i.d./100mg Qhs: mean 1.90 versus 1.10 on control; difference 0.80 (95% CI 0.16 to 1.44), standardized effect d = 0.18; z-test p = 0.014.

8. Statistical Interpretation

9. Statistical Methods Explained

The main result is a continuous outcome: change in satisfying sexual events per 28 days. For a continuous outcome, the mean gives the average observed change within an arm. Comparing arm means gives an estimate of the difference in average change between the active regimen and placebo. A mean difference of 0 would represent equal arm means; a positive difference in these reported comparisons means the active-arm mean change was higher than the placebo mean change. This direction describes the arithmetic of the endpoint, not a judgment about clinical importance.

The registry also reports standard deviations for the arm-level results. A standard deviation describes how dispersed individual measurements are around the group mean. It is not the uncertainty of the mean itself, and it is not a confidence interval. The posted arm means and standard deviations form the basis of the simple unadjusted comparisons. The registry does not report an individual-participant analysis or adjusted estimates that account for other covariates.

The posted comparison estimates are simple unadjusted recalculations from the summary statistics. Their p-values are explicitly unadjusted. The p-value measures how incompatible the observed data are with a specified null model of no mean difference, under the assumptions of the test. 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 test procedure and the confidence-interval level are not reported in the registry record. Consequently, the recalculated values are useful for reading the posted summaries but should not be mistaken for the trial sponsor’s prespecified analysis.

Precision can be understood through the confidence interval around a mean difference. It expresses a range of values compatible with the observed data under the method used to construct it. A narrower interval indicates greater statistical precision; a wider interval leaves more uncertainty about the size and direction of the difference. If an interval spans zero, the data are compatible with no mean difference as well as differences in either direction. If the entire interval lies above zero, the interval excludes zero under its stated construction. Here, the first two intervals span zero and the interval for the 50mg b.i.d./100mg Qhs comparison lies above zero. The record does not name the confidence level or provide a sponsor analysis to confirm these comparisons.

Variability matters for continuous outcomes because greater spread can make the group mean less precise, all else equal. General statistical explanation: when individual measurements vary substantially, it can be harder to distinguish a modest difference in averages from random variation. The standard deviation for the 50mg b.i.d./100mg Qhs arm is 5.3, compared with 3.4 in placebo; this descriptive contrast does not establish why the variability differs. It is one reason to consider both the estimated mean difference and its interval rather than focusing only on the difference in arm means.

The trial used a Full Analysis Set defined as participants with at least one post-dose, on-treatment efficacy assessment, and states that efficacy endpoints were analyzed primarily in that set. This definition identifies who was eligible for the efficacy analysis, but it does not clarify the specific approach to missing follow-up observations. The registry does not report whether a particular imputation method, repeated-measures model, or other missing-data method was used. It also does not report whether the primary comparison was adjusted for baseline value or other factors.

Multiple comparisons are relevant because each flibanserin regimen is compared with the same placebo group. If several hypotheses are tested, the chance of obtaining at least one small p-value by chance can increase. General statistical explanation: a multiplicity strategy may control that risk by adjusting thresholds or p-values, or by specifying a testing sequence. The registry does not report such a strategy. Thus the posted unadjusted p-values should be interpreted as unadjusted, rather than as evidence that a multiplicity-adjusted threshold was met.

The registry gives a diary algorithm that scales events to a 28-day period using the sum of events and the sum of days entered. This creates a standardized monthly measure from diary entries. General statistical explanation: diary outcomes can depend on both the event records and the completeness of diary days; incomplete recording can affect the estimate if entered days do not represent the unrecorded days. The registry does not report diary completion rates or enough detail to assess whether missing entries were balanced across arms.

Finally, a planning calculation based on an observed effect is different from the trial’s original design calculation. The posted planning figures use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation, with the target effect expressed as a stated fraction of the observed effect. They are illustrations of requirements under those assumptions, not evidence about the trial’s actual power. The original sample-size justification and the sponsor’s planned analysis assumptions are not reported in the registry record.

10. Confidence Intervals and Precision

The reported mean differences were 0.3 SSEs per 28 days for Flibanserin 25 mg b.i.d and Flibanserin 50mg Qhs/b.i.d, and 0.8 for Flibanserin 50mg b.i.d./100mg Qhs, each versus placebo. The confidence intervals for the first two comparisons extend across zero, so they allow for no mean difference as well as differences in either direction. The interval for the third comparison is entirely above zero. These features describe the intervals’ relationship to zero without implying that the registry reports a sponsor-adjusted result.

Interval width represents uncertainty about the estimated mean difference. The first two intervals are wider than the central estimates, leaving substantial uncertainty about the magnitude of any difference. The third comparison has a larger estimated difference, but its interval also spans a range of possible magnitudes. A point estimate is not a guarantee that the true effect equals that value. Confidence intervals also do not show the range of individual participant outcomes; the standard deviations describe participant-level spread, while intervals describe uncertainty in the estimated group contrast.

The registry does not report the confidence level or the method used for these intervals. Their statistical interpretation therefore cannot be fully checked against a prespecified analysis plan. Nor does the record supply an established threshold for a clinically important difference in SSEs per 28 days. Statistical precision and clinical importance are separate questions: an interval’s relation to zero addresses uncertainty about a statistical contrast, while clinical importance requires a meaningful-change criterion that is not reported in the registry record.

The comparisons are unadjusted recalculations from posted summary statistics. Their intervals do not incorporate a reported adjustment for the set of active-versus-placebo comparisons. The absence of an adjustment is important when interpreting the evidence collectively; each interval is not a standalone confirmation of a prespecified sponsor conclusion. The registry does not report sponsor inferential results for comparison with these recalculations.

11. Planning a Similar Trial: Sample Size

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

The sample-size values are planning illustrations expressed as participants per arm for 80% power and participants per arm for 90% power. They are not total trial enrollment figures. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a target effect equal to the stated fraction of the observed effect. The original trial’s design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the chosen effect under the stated assumptions, if that effect and those assumptions held. The 90% column uses a higher target probability of detection and therefore gives a larger planning requirement for the same effect scenario. These are prospective planning interpretations, not descriptions of what happened in this completed trial.

Rows for planning at 100%, 75%, and 50% of the observed effect show how the assumed effect size changes the estimate. A smaller target effect requires more participants to distinguish it from random variation under the same assumptions. For example, the posted figures for the 50mg b.i.d./100mg Qhs comparison are 484 participants per arm for 80% power and 648 for 90% power when planning for 100% of the observed effect; the corresponding figures are larger in the rows planning for 75% and 50% of that effect. Values differ by comparison because the observed mean differences and variability differ.

The curve represents the planning relationship between the assumed effect and the participant requirement; it should be read as an illustration alongside the listed assumptions, not as an observed trial outcome. These figures are not observed power. They do not show the probability that this completed trial detected an effect, and they should not be substituted for the unavailable original design rationale.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.300; pooled standard deviation σ = 3.450.
2. n = 2 × (1.96 + 0.842)² × 3.450² / 0.300² = 2,076.1, rounded up to 2,077 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.3                      # observed difference in means
sigma <- 3.45003119287175                     # 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(360555)
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 = 2,077 (80% power), 2,780 (90% power)
 75% of observed effect: n per arm = 3,691 (80% power), 4,941 (90% power)
 50% of observed effect: n per arm = 8,305 (80% power), 11,118 (90% power)
power.t.test: 2077 
Simulated power at n = 2,077 per arm: 0.801 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary efficacy endpoint and reports comparisons of each flibanserin regimen with placebo. It also lists two outcome measures, but no secondary outcome results are posted. The lack of posted secondary results means that the registry record cannot support a broader account of other efficacy outcomes or their relation to the primary endpoint.

Each reported unadjusted comparison addresses one active regimen versus placebo. When several comparisons are considered together, chance findings can become more likely if each is assessed independently at the same threshold. General statistical explanation: multiplicity procedures are used to manage that issue, for example by adjusting significance criteria or by defining an ordered testing plan. The registry record does not report whether any such procedure was prespecified or used. The unadjusted p-values should therefore not be read as multiplicity-adjusted evidence.

The record contains no analysis entries. It does not report the sponsor’s statistical analysis plan, the specific model used for the primary endpoint, the test underlying the posted p-values, or a prespecified confidence level. It also does not report interim analyses, a hierarchy among outcomes, or a rule for selecting among regimen comparisons. These are unknowns in the registry record, not evidence that a particular method was or was not used outside the record.

The stated Full Analysis Set included participants with at least one post-dose, on-treatment efficacy assessment, and the record says efficacy endpoints were analyzed primarily in that set. It does not provide enough information to determine how many participants lacked post-baseline data, how withdrawals were handled, or whether all randomized participants were included in a separate analysis. The specific method for incomplete eDiary records is also not reported. Missingness can matter for a diary-based outcome if recording completeness differs by arm or relates to the outcome; whether that occurred cannot be assessed from the posted information.

Without the analysis plan, multiplicity approach, and missing-data details, the posted estimates can be described and their uncertainty discussed, but a complete reconstruction of the sponsor’s confirmatory inference is not possible from the registry record.

14. 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: intervertebral disc protrustion (1.0%), appendicitis (0.8%), cholelithiasis (0.8%), ovarian cyst (0.5%), cholecystitic acute (0.3%).

The registry lists serious adverse events by arm as affected participants over the number at risk: 7 of 396 for Flibanserin 25 mg b.i.d, 6 of 392 for Flibanserin 50mg Qhs/b.i.d, 3 of 395 for Flibanserin 50mg b.i.d./100mg Qhs, and 8 of 398 for placebo. These are counts, not event rates calculated for a common exposure period. The registry does not provide the timing of the events or person-time at risk, so the figures should be read as the listed affected counts and their arm-specific denominators.

The record also lists other adverse events affecting 168, 293, 266, and 133 participants in the respective flibanserin and placebo arms, with the same arm-specific at-risk counts used in the serious-event listing. These figures are distinct from the serious adverse event counts. The record does not provide additional detail in this summary about severity grading, duration, relatedness, or whether a participant could contribute more than one event term.

Listed serious-event terms include “Intervertebral disc protrustion” at 1.0%, appendicitis and cholelithiasis at 0.8% each, ovarian cyst at 0.5%, and acute cholecystitis and intervertebral disc degeneration at 0.3% each. Death counts are not reported in the registry record. These descriptive safety listings do not by themselves establish a causal relationship to treatment or support a comparison of overall safety across regimens.

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

The posted endpoint results describe average changes in satisfying sexual event frequency from baseline to 28 weeks among participants meeting the Full Analysis Set definition. The placebo mean change was 1.1 SSEs per 28 days. Mean changes were 1.4 in each of the first two flibanserin arms and 1.9 in the 50mg b.i.d./100mg Qhs arm. The corresponding unadjusted mean differences versus placebo were 0.3, 0.3, and 0.8 SSEs per 28 days. These are group averages and do not describe the experience of every participant.

The uncertainty differs across comparisons. The intervals for the first two differences extend across zero, whereas the interval for the third lies above zero. The unadjusted p-values were 0.232, 0.227, and 0.014, respectively. Because no multiplicity adjustment or sponsor analysis is reported, these results should be treated as descriptive comparisons with uncertainty, not as a complete confirmatory conclusion across the set of regimens.

The result does not identify a threshold for a meaningful change, since such a threshold is not reported in the registry record. It also does not show whether any observed mean difference corresponds to an important difference for an individual. Means and standard deviations cannot reveal all features of the distribution, and the record does not provide the underlying diary data or participant-level response patterns.

The efficacy findings are limited to the stated analysis population and follow-up period. The registry does not report sufficient information about missing diary data, withdrawals, adherence, or the handling of incomplete assessments to establish how those factors affected the estimates. The reported safety counts are descriptive and do not establish that an event was caused by a study regimen. The results should not be converted into medical advice or a treatment recommendation.

In short, the registry records higher average change than placebo for each listed flibanserin regimen, with uncertainty that differs across comparisons. It does not provide the full sponsor analysis, adjusted multiplicity results, or enough methodological detail to make a comprehensive judgment about the trial’s confirmatory findings.

16. Why This Trial Matters Statistically

This trial is statistically informative because it reports a continuous, diary-derived endpoint across several randomized arms with a shared placebo comparator. The registry gives both means and standard deviations, allowing readers to distinguish the average change from the spread of observations. It also reports mean-difference estimates and confidence intervals, making uncertainty visible rather than presenting the arm means alone.

The pattern illustrates why estimates and precision should be read together. The first two active-versus-placebo differences are both 0.3 SSEs per 28 days, with confidence intervals that span zero. The third estimate is 0.8, with an interval above zero, but the larger standard deviation in that arm signals more variation in the endpoint. A reader therefore needs more than a point estimate or a single p-value to understand the evidence.

The example also highlights multiplicity. Multiple active regimens are compared with the same placebo, yet the registry does not report whether the comparisons were adjusted or how they fit into a prespecified testing strategy. The unadjusted p-value of 0.014 for one comparison is consequently not enough to infer the sponsor’s overall confirmatory conclusion. The registry’s absence of analysis entries makes that distinction especially important.

Finally, the registry separates the trial’s observed results from planning illustrations based on those results. A sample-size estimate derived from an observed effect can demonstrate how assumptions about effect size and desired power influence planning, but it cannot substitute for the original design rationale. This distinction is useful when interpreting completed trials: observed estimates, uncertainty, analysis choices, and prospective design calculations answer related but different statistical questions.

17. Limitations

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

The registry record leaves several trial-specific limitations unresolved. Although the design is described as randomized and double-masked, the method used to generate the allocation sequence and conceal it is not reported. The details of maintaining masking, including whether the masking was assessed, are also not reported. These omissions limit evaluation of how those design protections were implemented.

The record gives baseline-to-28-week endpoint results but does not provide a complete account of follow-up, diary completion, withdrawal, or adherence. It does not report the number of participants with incomplete diary records or the approach used to handle missing observations. Since the endpoint was derived from eDiary entries and days entered, missing recording could affect the monthly measure; its impact cannot be determined from the registry information.

The active-arm labels contain abbreviations and combined dose descriptions, while the detailed titration sequence is not reported. Therefore, the exact timing and progression of doses cannot be reconstructed from the posted record alone. The population is described as premenopausal women with hypoactive sexual desire disorder, with the official title specifying younger women in North America; the registry summary does not provide enough detail to judge how closely the enrolled population represents other settings or populations.

The registry reports no analysis entries or secondary outcome results. It does not provide the prespecified statistical analysis plan, the primary model, the confidence-interval level, a multiplicity method, or the sponsor’s inferential results. It also does not report the original sample-size justification or interim-analysis plan. The posted recalculations and safety counts should therefore be interpreted within these documentation limits, rather than as a full reconstruction of trial conduct and analysis.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Uptitration Trial of Flibanserin Versus Placebo in Premenopausal Women With Hypoactive Sexual Desire Disorder — NCT00360555.
• Registry record last updated 2016-06-27; status last verified 2016-06.
• Results first posted 2016-06-27.
• 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.

21. Record Summary

NCT00360555 is a completed phase 3 randomized, double-masked, parallel-group trial sponsored by Sprout Pharmaceuticals, Inc. The registry lists enrollment of 1584, a start of 2006-07, and primary completion in 2008-03. The study assessed flibanserin regimens against placebo in premenopausal women with hypoactive sexual desire disorder.

The primary outcome was change from baseline to 28 weeks in eDiary-recorded satisfying sexual events per 28 days. The registry posts arm means, standard deviations, and unadjusted recalculated comparisons with placebo. It reports no analysis entries or secondary outcome results. The sponsor’s statistical analysis plan, multiplicity approach, and detailed missing-data methods are not reported in the registry record.

The posted estimates describe average changes and their uncertainty; they do not, on their own, establish clinical importance or provide a treatment recommendation. Safety listings are descriptive, and death counts are not reported in the registry record.