A Safety & Efficacy Study of BGS649 in Women With Refractory Endometriosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Safety & Efficacy Study of BGS649 in Women With Refractory Endometriosis (NCT01116440), a randomized phase 2 study. The primary outcome is Mean Change in Baseline to Week 12 in Numeric Rating Scale Pelvic Pain Score.

2. Clinical Question

3. Trial Design

This was a Phase 2, randomized, double-blind, controlled, multicenter study with a parallel-group design. The official title describes oral BGS649 versus placebo, with both treatments co-administered with a combined oral contraceptive. The registry record lists BGS649 and placebo as the drug interventions and identifies Levora 28™ in the arm descriptions. Randomization and double masking are recorded, but the method used to generate the allocation sequence, conceal allocation, and maintain masking is not reported in the registry record.

Enrollment was 27. The primary endpoint is reported at 12 weeks, and the primary completion date is listed as 2011-07. The recorded study start is 2010-04-15. The study status is terminated. The reason for termination and the timing or circumstances of the decision are not reported in the registry record; termination alone does not establish why the study stopped or how that affected the results.

The primary population is described as the full analysis set, including all randomized patients except those randomized inadvertently who did not receive study drug. The primary endpoint has 11 participants in the BGS649 group and 16 in the placebo group. The registry record does not provide a protocol-level account of other analysis populations, exclusions beyond that definition, treatment adherence, or handling of participants who did not complete follow-up.

The study sought information on efficacy, safety, tolerability and pharmacokinetics. The posted results include the primary continuous pain outcome, four secondary pain outcomes, and adverse-event counts. The original statistical analysis plan, planned sample-size rationale, dose-level details, and any interim analysis plan are not reported in the registry record. The posted results therefore support description of the recorded outcomes, but not reconstruction of every design or analysis decision.

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.

Treatment

Reasons for not completing this period:

Withdrawal

Reasons for not completing this period:

Follow-up

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set. All patients randomised excluding those who were randomised inadvertently and did not receive study drug

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: Full Analysis Set.

6. Primary Endpoint

The registry lists the primary outcome as Mean Change in Baseline to Week 12 in Numeric Rating Scale Pelvic Pain Score, measured over 12 weeks.

The primary endpoint is mean change from baseline to Week 12 in Numeric Rating Scale pelvic pain score. The scale ranges from 0, meaning no pain, to 10, meaning the worst pain imaginable. It represents pain on a numerical continuum, and the endpoint summarizes the average within-person change in each treatment group over the stated follow-up period.

A change score is used to describe whether scores at follow-up are higher or lower, on average, than at baseline. A negative mean change indicates a decrease in the recorded score. The endpoint is intended to capture pelvic pain over time in the study population; the registry record does not specify a threshold for a response considered important to patients or clinicians.

The posted primary results give a mean and standard deviation for each group. The BGS649 group mean change was -0.764, with a standard deviation of 2.124, among 11 participants. The placebo group mean change was -2.171, with a standard deviation of 2.272, among 16 participants. These arm summaries describe observed data, not an adjusted effect or a conclusion about the clinical importance of the difference.

Baseline scores, the timing and method of pain-score collection, and how missing Week 12 scores were handled are not reported in the registry record. Those details would help readers assess comparability at baseline and understand how the reported averages relate to the full randomized population.

7. Results Posted in the Registry

• BGS649 Co-administered With Levora 28™: mean -0.76 versus -2.17 on control; difference 1.41 (95% CI -0.27 to 3.08), standardized effect d = 0.64; z-test p = 0.100.

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.

Mean Change From Baseline to 4 Weeks in Numeric Rating Scale Pelvic Pain Scores

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • BGS649 Co-administered With Levora 28™: mean -0.66 versus -0.93 on control; difference 0.27 (95% CI -0.68 to 1.22), standardized effect d = 0.23; z-test p = 0.579.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BGS649 Co-administered With Levora 28™ and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Patients Achieving a Response in Numeric Rating Scale Pelvic Pain Score

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • BGS649 Co-administered With Levora 28™: 9.1% (1/11) versus 37.5% (6/16) on control; risk difference -28.4 percentage points (95% CI -57.6 to 0.8), risk ratio 0.24 (0.03–1.74); unadjusted two-proportion z-test p = 0.098.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BGS649 Co-administered With Levora 28™ and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline in Numeric Rating Scale Pelvic Pain Scores

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • BGS649 Co-administered With Levora 28™: mean -1.28 versus -2.06 on control; difference 0.78 (95% CI -0.88 to 2.43), standardized effect d = 0.36; z-test p = 0.359.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BGS649 Co-administered With Levora 28™ and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the description of pelvic pain beyond the primary Week 12 mean-change endpoint. They include mean change at earlier follow-up, a response measure based on the Numeric Rating Scale, and response on the modified Biberoglu & Behrman scale. Together, these outcomes ask whether the pattern depends on when pain is assessed, whether results are summarized as an average or as meeting a response criterion, and which scale is used.

Across the posted secondary results, the direction of the group summaries is not more favorable to BGS649 than to placebo: the mean-change summaries are more negative in the placebo group, and the response percentage is higher in the placebo group. This broad pattern is consistent with the primary point estimate's direction, but the outcomes differ in definition and follow-up. It should not be treated as several independent confirmations of a single conclusion, since the same small study population contributes to multiple measures.

The secondary comparisons are unadjusted, and the registry record reports no secondary analyses. Multiple endpoints create an opportunity for chance findings when results are examined together. Without a prespecified hierarchy or multiplicity adjustment, individual unadjusted results carry less inferential weight than a clearly specified primary analysis. Conversely, a lack of a small p-value on a secondary comparison would not establish that groups are equivalent.

The registry record does not report the original statistical analysis plan, whether these outcomes were prespecified in their posted form, or how missing secondary measurements were handled. The response definitions and thresholds also matter to interpretation. Accordingly, the secondary outcomes are best viewed as supporting descriptive context for the primary result and as potential inputs to future research planning, rather than as stand-alone evidence of a definitive treatment effect.

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

• Mean Change From Baseline to 4 Weeks in Numeric Rating Scale Pelvic Pain Scores
• Percentage of Patients Achieving a Response in Numeric Rating Scale Pelvic Pain Score
• Mean Change From Baseline in Numeric Rating Scale Pelvic Pain Scores
• Percentage of Patients Achieving a Response in Their Pelvic Pain Score Measured on the Modified Biberoglu & Behrman Scale

9. Statistical Interpretation

10. Statistical Methods Explained

A mean summarizes the average score change across participants in an arm. For this primary endpoint, the registry reports a mean change and a standard deviation for each group. The mean describes the central tendency of the observed changes; the standard deviation describes how widely individual changes vary around that mean. These are different quantities: the standard deviation is not the uncertainty interval for the mean and does not show the range of participant outcomes.

The treatment contrast is expressed as the BGS649 mean minus the placebo mean. For the primary endpoint, the unadjusted recalculated difference is 1.407. A positive contrast means the BGS649 mean change is numerically higher than the placebo mean change. Because decreases are represented by negative changes, a higher change value in this comparison corresponds to a smaller decrease in the BGS649 group. The contrast is a difference in average change, not a ratio, and it does not describe how every participant's score changed.

The posted confidence interval gives a range of values compatible with the observed data under the assumptions of the interval calculation. In general, a confidence interval communicates uncertainty about an estimate: a narrower interval indicates greater precision, while a wider interval indicates less precision. Here, the interval includes zero and extends in both directions, so the result does not precisely distinguish the groups. The method used to construct the registry's comparison interval is not reported in the registry record. The interval quoted in the statistical display is a simple unadjusted recalculation from the arm summaries, not a claim about an adjusted trial analysis.

The unadjusted p-value is 0.1. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. The registry record does not report the test procedure, its assumptions, or a prespecified threshold for interpreting the primary comparison. The recalculated p-value should therefore be read as a descriptive, unadjusted statistic rather than as a substitute for an analysis plan.

For continuous outcomes, a mean difference is interpretable in the units of the score. The Numeric Rating Scale uses score units on a 0-to-10 scale. The observed mean difference is in units of change on that scale, not a percentage. In general, continuous outcomes can be summarized with means when those summaries are appropriate to the data, but the registry record does not provide participant-level distributions or diagnostics for the pain scores. It is therefore not possible to assess skewness, influential observations, or other distributional features from the posted arm summaries alone.

Secondary binary response outcomes are expressed as percentages of participants meeting a response definition. A risk difference compares those proportions by subtraction and retains percentage-point interpretation when expressed in percentage units. In general, binary measures summarize whether a criterion was met, rather than the size of each participant's change. Their meaning depends on the response definition and its handling of missing observations. The registry record lists response outcomes but does not provide a complete account of the response threshold or missing-data rules.

Simple unadjusted recalculations are not equivalent to the trial's planned or sponsor-conducted analyses. They use the posted summary statistics to describe an unadjusted group contrast. They do not incorporate covariate adjustment, stratification, repeated measurements, or missing-data assumptions unless those are explicitly part of the calculation; such features are not reported for the primary analysis in the registry record. No reported analyses are listed for the secondary outcomes. No reported analysis count is available for interpreting the secondary results as formal sponsor analyses.

For general planning, over-dispersion matters when observed variability is greater than a model expects: it can make standard errors too small if the model does not account for that extra variation. This is a general statistical consideration, not a finding established by the posted summaries. The primary endpoint is continuous, and the registry does not report a model-based variance assessment. More generally, statistical assumptions should be evaluated against the data and analysis plan; those materials are not reported in the registry record.

The sample-size illustrations use the observed effect as a planning reference and apply a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. They consider fractions of the observed effect. These assumptions describe the illustrations, not the original study's sample-size justification or design. The original planning rationale is not reported in the registry record, and a planning calculation based on an observed estimate cannot establish what the trial was designed to detect.

11. Confidence Intervals and Precision

The primary mean-difference estimate is 1.407, with a 95% confidence interval extending from approximately -0.271 to 3.085. The interval is wide relative to the point estimate and crosses zero. This indicates limited precision: the posted data are compatible with effects on either side of no difference, as well as with effects of varying magnitude. The point estimate alone should not be read as a precise measurement of the treatment contrast.

In general, a confidence interval is a range generated by a statistical procedure that, under its assumptions, reflects uncertainty in an estimate. It is not a range containing a fixed proportion of individual participant outcomes, and it does not assign a probability to the true effect after the data have been observed. The interval for the primary result is an unadjusted recalculation from the posted arm summaries. The method used for any sponsor interval is not reported in the registry record.

The endpoint groups are small: the primary result includes 11 BGS649 participants and 16 placebo participants. The standard deviations, 2.124 and 2.272, show substantial spread in observed changes within the groups. Small groups combined with variable outcomes tend to produce less precise estimates than larger groups with similar variability. This is a general statistical relationship, not an additional trial result.

Precision is distinct from clinical importance. The registry record does not report a threshold for a clinically important difference on the scale, so the interval cannot be classified as excluding or including a meaningful benefit using a registry-defined criterion. It also does not report the handling of missing scores or the confidence-interval method. Those omissions limit how fully the interval's assumptions and practical meaning can be assessed.

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 sample-size illustrations describe participants per arm, not total events. They use the observed effect as a reference and show planning for 100%, 75%, and 50% of that observed effect. For example, the primary endpoint illustrations list 39 participants per arm for 80% power and 53 participants per arm for 90% power when planning for 100% of the observed effect. The corresponding figures are 70 and 93 when planning for 75%, and 156 and 209 when planning for 50%.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. In plain language, the 80% power column represents the planned group size for a design with an 80% chance of detecting the assumed effect under those assumptions, if that effect and the model assumptions are correct. The 90% power column represents a higher target chance of detection under the same stated framework.

Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm when the planned effect is a smaller fraction of the observed one. These are planning illustrations based on this study's observed estimate, not observed power. The original study's sample-size justification and its design assumptions are not reported in the registry record. The illustrations should not be read as proof that a future study will achieve the stated power, since actual precision and power depend on the effect, variability, analysis and study conduct.

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 = 1.407; pooled standard deviation σ = 2.214.
2. n = 2 × (1.96 + 0.842)² × 2.214² / 1.407² = 38.9, rounded up to 39 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 <- 1.4069                      # observed difference in means
sigma <- 2.21421706045275                     # 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(1116440)
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 = 39 (80% power), 53 (90% power)
 75% of observed effect: n per arm = 70 (80% power), 93 (90% power)
 50% of observed effect: n per arm = 156 (80% power), 209 (90% power)
power.t.test: 39.9 
Simulated power at n = 39 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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes or comparisons. Even when each analysis is considered separately, examining multiple outcomes can increase the chance of finding an apparently notable result by chance. The registry record lists five outcome measures, including the primary endpoint and four secondary outcomes. It does not report a hierarchy for testing, a multiplicity adjustment, or a plan for controlling an overall error rate. The unadjusted secondary comparisons therefore need cautious interpretation and should not be read as if each were the sole prespecified test.

The record lists no reported analyses for the secondary outcomes. The comparisons described for those endpoints are simple unadjusted recalculations from the arm summaries, not reported sponsor analyses. The original analysis plan, including any planned covariate adjustment or repeated-measures approach, is not reported in the registry record. This limits assessment of whether the posted outcome summaries correspond to the originally intended inferential questions.

The primary population is defined as the full analysis set, with patients randomized inadvertently and not receiving study drug excluded. The record does not explain how that exclusion was decided or report all other details of the analysis population. The primary outcome groups contain 11 and 16 participants, while the safety groups at risk contain 12 and 15. These are different reported populations for different outcomes; the registry record does not provide enough detail to reconcile all participant flow between them.

Missing-data procedures are not reported in the registry record. It is not clear whether all randomized participants had Week 12 assessments, whether any scores were imputed, or how participants without a measurement were treated in the analysis. Missingness can affect both the estimate and its uncertainty, particularly if the chance of having an observed score is related to symptoms or treatment. Without participant flow and missing-data methods, the potential influence cannot be assessed from the posted summaries alone.

Interim analyses and any associated decision rules are also not reported in the registry record. These omissions do not prove that such procedures were or were not used; they mean that readers cannot evaluate them from the record. The reason for termination is likewise not reported. Clear reporting of multiplicity, missingness, analysis populations, and study conduct would be needed to make a more complete assessment of how the posted estimates were generated.

15. 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: pregnancy (8.3%), endometriosis (6.7%), pelvic pain (6.7%).

The serious adverse-event counts are reported among participants at risk. In the BGS649 group, 12 participants were at risk and 1 was affected by a serious adverse event. In the placebo group, 15 were at risk and 2 were affected. These are participant counts, not event rates calculated for a particular time at risk, and the registry record does not provide follow-up exposure details for interpreting them further.

The listed serious-event terms include Pregnancy at 8.3%, Endometriosis at 6.7%, and Pelvic pain at 6.7%. The record does not establish from these labels alone whether an event was caused by study treatment. Seriousness and causality are distinct assessments; a serious event is not necessarily treatment-related. The number of deaths is not reported in the registry record.

Other adverse events affected 10 of 12 participants at risk in the BGS649 group and 10 of 15 at risk in the placebo group. The small groups and lack of detail on event timing, duration, severity and attribution limit comparisons. These counts describe the posted safety record but are not sufficient to characterize every safety aspect of treatment or to establish a difference between groups.

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

The posted results describe average pelvic pain score changes over the study follow-up in a small randomized study. The primary group means both decreased from baseline, while the mean decrease was larger in the placebo group. The unadjusted mean difference favors the placebo group in direction, but its confidence interval is broad and includes zero. The data do not provide a precise estimate of the between-group difference.

These results do not establish that BGS649 caused a particular change, that the groups are equivalent, or that the observed difference would recur in another population. A confidence interval spanning zero is not proof of no effect. Nor does a point estimate in one direction establish a clinically important difference. The registry record does not report a clinically important threshold for the Numeric Rating Scale or enough detail about the analysis to resolve those questions.

The study compared BGS649 with placebo while both groups received Levora 28™. Its contrast therefore concerns adding the study drug within that concurrent-treatment context, not comparing the contraceptive with no contraceptive. The record does not report sufficient dose details to draw conclusions across dose levels, and it does not establish whether the results apply to people outside the study population or to other treatment settings.

Safety counts should also be interpreted descriptively. The reported serious events and other adverse events occurred among small groups, and causal attribution, timing and exposure duration are not fully reported. The counts do not prove that an event was caused by a treatment, nor do they rule out risks that the study was too small to characterize.

Overall, the registry record supports a cautious reading of observed group summaries, not a clinical recommendation. It leaves important questions about missing data, analysis choices, study termination and the original design assumptions unanswered. Those limitations matter when considering how much confidence to place in any single estimate.

17. Why This Trial Matters Statistically

This study illustrates why a treatment comparison should be read through both its point estimate and its uncertainty. The primary mean difference is a compact summary, but the confidence interval shows that the estimate is imprecise and compatible with values in either direction. The unadjusted p-value alone cannot convey that range or the possible clinical relevance of the difference.

It also shows how a small randomized study can produce useful descriptive information while leaving substantial uncertainty. Randomization and double masking are important design features recorded for this study, but they do not make a small sample precise or remove the need for transparent reporting of analysis methods and missing data. Readers need to consider the size of the endpoint groups and the variability in observed scores alongside the estimated contrast.

The secondary outcomes demonstrate the challenge of interpreting multiple related endpoints. Different scales, time points and response definitions can offer complementary views, but a consistent-looking set of descriptive results does not replace a prespecified analysis strategy. When multiplicity methods and the original plan are unavailable, secondary comparisons should carry limited confirmatory weight.

The sample-size illustrations are useful for showing how assumptions about the effect size influence planning, but they are not evidence about the original design or proof of the study's ability to detect a particular effect. Their value lies in explaining the relationship between smaller targeted effects and larger planned groups, while reminding readers that planning depends on assumptions about variability and analysis.

More broadly, this record is a practical example of separating what is recorded from what remains unknown. The posted means, standard deviations, intervals and adverse-event counts can be described directly. Causal interpretation, generalization and claims about the original protocol require details that are not reported in the registry record.

18. 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 primary endpoint groups are small, with 11 participants in the BGS649 arm and 16 in the placebo arm. The observed standard deviations indicate appreciable variation in pain-score change. Together, small groups and variable outcomes limit precision and make the estimates potentially sensitive to individual observations; participant-level data are not reported.

The record does not report the baseline score distribution, missing-data methods, adherence, timing of measurements, or the handling of participants who did not complete follow-up. It also does not provide a detailed account of participant flow beyond the primary population definition. These omissions make it difficult to assess whether the posted averages represent all participants as intended or whether missing observations could affect the comparison.

The registry record is marked terminated, but the reason for termination is not reported. The original sample-size justification, analysis plan, interim analysis procedures, and multiplicity strategy are also not reported in the registry record. As a result, the posted unadjusted comparisons cannot be assessed against a full prespecified analysis framework.

The primary endpoint's confidence interval is based on a simple unadjusted recalculation from the posted summaries. The method used for any sponsor analysis is not reported, and no secondary analyses are listed. The registry record also does not specify a clinically important difference threshold for the pain scale or provide enough detail to determine how the response definitions were applied in all cases.

Safety interpretation has similar constraints. Counts at risk differ between the safety groups and the primary endpoint groups, while event timing, exposure, severity detail and causal attribution are not fully reported. The number of deaths is not reported in the registry record. These gaps limit both efficacy and safety interpretation, without themselves establishing that any particular bias or harm occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Safety & Efficacy Study of BGS649 in Women With Refractory Endometriosis — NCT01116440.
• Registry record last updated 2020-11-23; status last verified 2020-11.
• Results first posted 2020-10-30.
• 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.

22. Record Summary

NCT01116440 is a Phase 2 randomized, double-blind, parallel-group study of BGS649 co-administered with Levora 28™ versus placebo co-administered with Levora 28™ in women with refractory endometriosis. The registry lists enrollment of 27 and a terminated study status.

The primary outcome is mean change from baseline to Week 12 in Numeric Rating Scale pelvic pain score. The posted arm means were -0.764 for BGS649 and -2.171 for placebo. The unadjusted recalculated mean difference was 1.407, with a confidence interval that crosses zero. The record also lists four secondary pain outcomes and adverse-event counts.

The registry record does not report the original sample-size rationale, full statistical analysis plan, missing-data procedures, multiplicity approach, or reason for termination. These limits, together with the small endpoint groups and imprecise primary estimate, support cautious interpretation of the posted results.