Efficacy, Safety, and Tolerability of JNJ-27018966 (Eluxadoline) in the Treatment of Irritable Bowel Syndrome With Diarrhea: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy, Safety, and Tolerability of JNJ-27018966 (Eluxadoline) in the Treatment of Irritable Bowel Syndrome With Diarrhea (NCT01130272), a randomized phase 2 study. The primary outcome is Percentage of Participants Who Were Composite Responders Based on Improvements From Baseline in Daily Worst Abdominal Pain and Daily Stool Consistency Scores at Week 4.

2. Clinical Question

The question is about a defined symptom-response measure, not every aspect of irritable bowel syndrome or every outcome collected. The registry also lists secondary measures involving pain, stool scores, daily bowel movements, and symptom response over time. The primary comparison focuses on the combined response at a particular follow-up point. The posted results give the response percentages for each dose and placebo, while the sponsor’s reported analyses give odds ratios and confidence intervals for the dose-versus-placebo comparisons.

3. Trial Design

The registry describes a randomized, double-blind, placebo-controlled, parallel-group, dose-ranging, multicenter study. Its phase was Phase 2, and its status is completed. The registered enrollment was 807. The study compared four eluxadoline dose groups with a matching-placebo group; each assigned treatment was taken orally twice daily for up to 12 weeks.

The registry records quadruple masking. That label indicates that masking was reported, but the registry record does not identify which participant, investigator, or other roles were included in the masking designation. The study’s parallel-group model means the listed arms represent separate treatment groups rather than a crossover sequence. Random allocation supports a planned comparison across groups, although the registry record does not report the allocation ratio or the method used to generate or conceal the assignment sequence.

The primary endpoint was assessed from baseline through Week 4. Its analysis population was defined as participants who received at least one dose and had baseline and at least one postrandomization daily pain rating and Bristol Stool Scale rating. This endpoint population included 754 participants. Arm-level primary results were reported for eluxadoline 5 mg, 25 mg, 100 mg, and 200 mg, and placebo.

The registered study dates run from 2010-04-28 for study start to 2011-07-14 for primary completion. The registry lists four secondary outcomes: changes in weekly pain scores, weekly Bristol Stool Scale scores, and daily bowel-movement counts, along with a response measure based on prespecified symptom improvement. The original sample-size justification, detailed allocation procedure, and full protocol-level analysis plan 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: 807 patients were randomized in the trial. 18 of these patients were enrolled at a site terminated by Furiex, reported to the FDA for potential scientific misconduct, and were excluded from all datasets. All Randomized Patients=789 patients.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to treat (ITT) set was defined as the 754 participants that received at least 1 dose of study drug and had baseline and at least 1 postrandomization daily pain rating and 1 postrandomization Bristol Stool Scale (BSS) rating.

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 patients.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Were Composite Responders Based on Improvements From Baseline in Daily Worst Abdominal Pain and Daily Stool Consistency Scores at Week 4, measured over Baseline (Week prior to Randomization) to Week 4.

The primary endpoint is the percentage of participants classified as composite responders at Week 4. The measure combines abdominal pain and stool consistency because both are central symptom domains in the registered question. Meeting only one component does not qualify as a response.

For the pain component, average daily worst abdominal pain over the past week had to improve by at least 30% and at least 2 points compared with the baseline average. Pain was recorded on an 11-point scale, from 0 for no pain to 10 for the worst pain imaginable. For the stool component, Bristol Stool Scale scores of 3 or 4 had to occur on 66% of reported days in the past week. The scale distinguishes stool consistency, with lower scores describing harder stools and higher scores describing looser stools.

The definition also required diary entries for at least 5 out of 7 days in the interval. This requirement makes the endpoint depend on both symptom values and sufficient diary completion. A participant without enough recorded days could fail the endpoint definition even if the available entries appeared favorable.

A composite endpoint is used to represent improvement across multiple aspects of the condition in one response classification. It is clinically interpretable as a joint symptom threshold, but it does not show the separate contribution of pain and stool consistency by itself. The registry lists separate secondary outcomes for changes in pain and stool scores, but those results are not included in the primary outcome figures described in this record.

7. Results Posted in the Registry

• Eluxadoline 5 mg: 12.4% (13/105) versus 5.7% (9/159) on control; risk difference 6.7 percentage points (95% CI -0.5 to 14.0), risk ratio 2.19 (0.97–4.93); unadjusted two-proportion z-test p = 0.053.
• Eluxadoline 25 mg: 12.0% (20/167) versus 5.7% (9/159) on control; risk difference 6.3 percentage points (95% CI 0.2 to 12.4), risk ratio 2.12 (0.99–4.51); unadjusted two-proportion z-test p = 0.045.
• Eluxadoline 100 mg: 11.0% (18/163) versus 5.7% (9/159) on control; risk difference 5.4 percentage points (95% CI -0.6 to 11.4), risk ratio 1.95 (0.90–4.21); unadjusted two-proportion z-test p = 0.081.
• Eluxadoline 200 mg: 13.8% (22/160) versus 5.7% (9/159) on control; risk difference 8.1 percentage points (95% CI 1.7 to 14.5), risk ratio 2.43 (1.15–5.11); unadjusted two-proportion z-test p = 0.015.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: each person either meets the composite responder definition or does not. The reported group result is the percentage classified as a responder. The comparison can therefore be expressed in several ways, including a difference in response proportions or an odds ratio. Each measure answers a related but distinct question, and values from different measures should not be treated as interchangeable.

What does an odds ratio describe?

An odds ratio compares the odds of meeting the response definition in one group with the odds in another group. An odds ratio above 1 indicates higher observed response odds in the eluxadoline group than in placebo for the reported comparison. It does not directly state the percentage-point difference in response, and it should not be read as a ratio of response percentages. For these data, the sponsor reported odds ratios above 1 for all four dose comparisons. Their uncertainty is described by the corresponding confidence intervals.

The registry identifies the sponsor’s method as ANCOVA and labels the reported estimates as odds ratios. ANCOVA is a model-based method that can compare groups while accounting for specified covariates or baseline information. The registry record does not give enough detail to identify the full model specification, the covariates included, or the exact procedure used to derive the odds ratios. Those details matter for reproducing or fully assessing a model-based estimate.

How does the unadjusted recalculation differ?

The recalculated comparisons are simple, unadjusted comparisons based on the posted group response summaries. They do not reproduce every aspect of the sponsor’s analysis. In particular, they do not incorporate an undocumented model specification. The recalculated p-values differ from the sponsor-reported p-values for some dose comparisons, and the record flags this discrepancy. The sponsor’s own analysis therefore takes precedence for interpretation of the reported trial analysis. The recalculations serve as a transparent summary-level check, not a replacement analysis.

A risk difference expresses the difference between two response proportions on the probability scale. It can be easier to understand in absolute terms than an odds ratio, while the odds ratio gives a relative comparison of odds. The recalculated risk-difference intervals are based on the posted summary statistics. Because of the stated discrepancy, those recalculated estimates should not be treated as the definitive trial estimates. No adjusted risk-difference analysis is reported in the registry record.

What does a p-value contribute?

A p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the analysis. It does not give the probability that the null hypothesis is true, the probability that a finding is due to chance, or the chance that a treatment will help an individual. A smaller p-value is not necessarily evidence of a larger effect. Interpretation should consider the estimated contrast, its confidence interval, the endpoint definition, and whether multiple comparisons were addressed.

The sponsor-reported p-values accompany the model-based comparisons. The registry does not report a multiplicity adjustment or an explicit hierarchy among the four dose comparisons. Without such information, the p-values should not be interpreted as if the handling of multiple comparisons were known. The registry record also does not report whether interim analyses were planned or conducted, or the trial’s original statistical analysis plan.

Why is the endpoint definition important?

Binary classification compresses several daily observations into a responder or nonresponder outcome. The composite requires both the pain and stool criteria, along with adequate diary completion. That can make the endpoint a stringent joint measure, but it also means the group percentage can be affected by missing diary entries. The response percentage does not reveal which component most often prevented response. Separate component-level distributions and missing-data analyses would help clarify that, but the registry record does not report those details for this primary result.

The primary analysis population is described by eligibility for the endpoint analysis: receipt of at least one dose plus baseline and postrandomization pain and Bristol Stool Scale ratings. This is not simply every enrolled participant. It is also not necessarily the same population used for safety reporting, where the adverse-event denominators vary by arm. The registry’s stated population definition should be kept in mind when comparing the efficacy and safety summaries.

In general, randomized allocation can reduce systematic differences between groups at the start of a trial, while masking can reduce some influences on care and outcome assessment. These design features do not eliminate uncertainty, missing data, model assumptions, or the possibility of chance findings across multiple comparisons. The registry confirms randomized allocation and quadruple masking, but does not report sufficient implementation detail to assess every potential source of bias.

10. Confidence Intervals and Precision

The sponsor-reported 95% confidence intervals indicate the range of values reasonably compatible with the model and observed data under its assumptions. They are not a guarantee that the true effect lies inside the particular interval, nor do they capture every source of uncertainty, such as possible bias or model misspecification. A narrower interval generally indicates greater statistical precision than a wider interval.

For eluxadoline 5 mg, the reported odds ratio was 2.457, with a 95% confidence interval from 0.994 to 6.077. For 25 mg, it was 2.383, with an interval from 1.036 to 5.478. For 100 mg, it was 2.079, with an interval from 0.893 to 4.842. For 200 mg, it was 2.797, with an interval from 1.227 to 6.376. Each interval is wide, so the estimates allow a substantial range of possible odds ratios.

The intervals for 5 mg and 100 mg include 1, the null value for an odds ratio. The intervals for 25 mg and 200 mg do not include 1. This is consistent with the sponsor-reported p-values, though the interval and p-value do not describe effect importance. The intervals do not show that the true odds ratio is exactly the point estimate, and the range of plausible values differs across comparisons.

The response percentages are relatively modest in all groups, including placebo. When outcomes are uncommon, the number of observed responders can be limited, which can contribute to imprecision. General statistical context: confidence intervals reflect sampling uncertainty under the analysis assumptions; they do not resolve concerns about missing data, multiplicity, or differences between the registry’s summary recalculations and the sponsor’s model-based analysis.

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 figures are planning illustrations based on the observed effect, not the trial’s own design calculations. The original design assumptions and sample-size justification are not reported in the registry record. For the binary outcome, the figures are participants per arm, not total events. The 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 set at the stated fraction of the observed effect.

The 80% power column gives the planned number of participants per arm for a design that would have an 80% chance of detecting the specified effect if that effect were the true one, under the planning assumptions. The 90% power column gives the corresponding per-arm planning number for a higher chance of detection. These are design calculations, not evidence that the completed study had a particular probability of finding a result.

Each dose-versus-placebo comparison has its own planning illustration because the observed contrast differs across comparisons. The rows for planning at 100%, 75%, and 50% of the observed effect show what happens when the target is reduced relative to the observed contrast. Smaller effects need more participants to detect with the same power and significance level. The values are therefore sensitive to the observed effect used as their starting point; they should not be treated as a guarantee that a future study will achieve its planned results.

This is not observed power. It is a forward-looking illustration using assumptions stated for the calculation, not a retrospective measure of how successful the completed trial was. The registry record does not report the trial’s own original design assumptions, and the planning figures should not be used to infer those assumptions.

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

Worked calculation for this trial

1. Control proportion p₀ = 0.057; treatment proportion p₁ = 0.124; average p̄ = 0.090.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4051 = 0.7941.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4023 = 0.3386.
4. n = (0.7941 + 0.3386)² / (0.0672)² = 284.1, rounded up to 285 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.0566037735849057                          # control proportion
p1 <- 0.123809523809524                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

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

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1130272)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 285 (80% power), 380 (90% power)
 75% of observed effect: n per arm = 463 (80% power), 620 (90% power)
 50% of observed effect: n per arm = 945 (80% power), 1,264 (90% power)
power.prop.test: 284.1 
Simulated power at n = 285 per arm: 0.816 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The sponsor reported ANCOVA analyses as odds ratios for each eluxadoline dose versus placebo, with 95% confidence intervals and p-values. Those results are the primary inferential results in the registry. The simple recalculations are unadjusted comparisons derived from the posted group summaries, and the registry flags a discrepancy between them and the sponsor’s reported analyses. Under that circumstance, the sponsor’s own analysis takes precedence.

The unadjusted p-values are 0.053 for 5 mg, 0.045 for 25 mg, 0.081 for 100 mg, and 0.015 for 200 mg. The sponsor-reported p-values are 0.052, 0.041, 0.090, and 0.015, respectively. The estimates are not identical across approaches for every comparison. This is a reason to distinguish the two analyses rather than select whichever result appears more favorable.

The registry identifies ANCOVA but does not report the complete model specification, the covariates, or enough methodological detail to reproduce the sponsor’s results. The recalculation is consequently a limited check using summary data, not a substitute for the trial’s analysis. The discrepancy should be kept visible when interpreting precision and statistical significance. Where a sponsor estimate and a summary-level recalculation differ, interpretation should emphasize the sponsor-reported analysis while acknowledging that the registry record does not provide enough detail to resolve the source of the difference.

14. Multiplicity, Missing Data and Analysis Populations

The primary endpoint involves four separate dose-versus-placebo comparisons. Testing several comparisons creates a multiplicity issue: even if each test is conducted at a conventional threshold, the chance of at least one apparently notable result can increase across a family of tests. General statistical practice may address this through a prespecified testing hierarchy or an adjustment to the inference, but the registry record does not report whether either approach was used. It also does not report a multiplicity-adjusted p-value or confidence interval. The reported p-values should therefore be read as the individual values stated in the registry, not assumed to control error across all dose comparisons.

The registry lists four secondary outcomes in addition to the primary outcome, and reports six outcome measures and eight analyses. It does not provide enough detail to determine the full number of statistical tests, their ordering, or how any secondary analyses were incorporated into a broader testing strategy. Interim analyses and stopping rules are not reported in the registry record. Their absence from the record should not be interpreted as evidence that none occurred.

For the primary analysis, the registry defines the population as participants who received at least one dose and had baseline plus at least one postrandomization pain and Bristol Stool Scale rating. That definition makes the presence of postrandomization measurements part of inclusion in the endpoint analysis. The registry does not report a missing-data imputation method, sensitivity analyses for missing diaries, or how participants without adequate diary completion were handled beyond the endpoint’s stated diary requirement.

These omissions matter because diary completion is part of the composite response definition. Missing observations can affect whether a participant has enough recorded days to qualify for evaluation, and the primary population definition requires postrandomization ratings. The record does not establish whether missingness differed by arm or whether results were robust to alternative assumptions about missing outcomes.

The posted enrollment is 807, while the defined primary endpoint population is 754. These are different reported quantities with different meanings; the first is registered enrollment and the second is the endpoint analysis population as defined in the registry. The registry does not report a full participant-flow explanation for the difference. A full intention-to-treat analysis conventionally includes all randomized participants in their assigned groups, but the stated endpoint population is more specifically defined by treatment receipt and available baseline and follow-up ratings. The record does not describe an alternative full-population analysis for this endpoint.

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: noncardiac chest pain (1.0%), anxiety (0.6%), depression (0.6%), pancreatitis acute (0.6%), pancreatitis (0.6%).

The registry reports serious adverse events and other adverse events by group. For serious adverse events, the reported affected-participant counts were 1 among 159 for placebo, 1 among 105 for eluxadoline 5 mg, 3 among 170 for 25 mg, 1 among 165 for 100 mg, and 3 among 172 for 200 mg. For other adverse events, the corresponding counts were 25 among 159, 20 among 105, 34 among 170, 27 among 165, and 43 among 172. These are descriptive counts with their reported group denominators, not adjusted comparisons.

The serious-event terms listed at the top include noncardiac chest pain at 1.0%, and anxiety, depression, acute pancreatitis, pancreatitis, and pneumonia at 0.6% each. The record does not give enough detail in these summaries to compare event severity, timing, duration, or causal attribution across treatment groups. The safety denominators also differ from some of the primary efficacy group counts, so the two sets should not be treated as if they describe identical analysis populations.

Deaths are not reported in the registry record. The adverse-event figures describe what was recorded during the trial; they do not by themselves establish whether an event was caused by treatment, and they do not provide a complete assessment of safety beyond the reported categories and terms.

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

The primary result describes the proportion meeting a specific combined symptom-response definition at Week 4. The posted percentages were higher in each eluxadoline group than in placebo, ranging from 11.0% to 13.8% across the dose groups, compared with 5.7% for placebo. The result is a group-level description of a defined endpoint; it is not a prediction that an individual participant will respond.

The sponsor’s reported odds ratios are above 1 for every dose comparison, but their confidence intervals are broad. The sponsor-reported p-values are below 0.05 for 25 mg and 200 mg, and above 0.05 for 5 mg and 100 mg. Because the trial compared multiple doses, and multiplicity handling is not reported, these individual p-values should not be read as a complete account of the evidence across all comparisons. The discrepancy between the sponsor analysis and the unadjusted recalculations also favors careful reliance on the sponsor’s stated analysis rather than treating the recalculations as definitive.

The percentages do not tell how much pain improved on average, how stool consistency changed separately, or how many participants met one component but not the other. The composite requires both symptom criteria and sufficient diary entries. It does not capture all possible experiences of the condition, nor does it answer every question about safety, duration, or outcomes beyond the reported follow-up.

General statistical context: a statistically notable comparison does not by itself establish clinical importance, and a comparison that does not cross a chosen threshold does not demonstrate no difference. Precision, endpoint relevance, missing-data handling, multiplicity, and the analysis population all shape interpretation. The registry record does not report enough detail to resolve these issues fully. The posted results therefore support a focused description of this Week 4 composite response, rather than broad conclusions about treatment effects outside the measured endpoint and trial context.

17. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through its endpoint definition rather than as a free-standing percentage. The primary response required improvement in both abdominal pain and stool consistency, plus adequate diary completion. That makes the result an example of a composite binary outcome: easy to summarize as a percentage, but less informative about which component drove the classification or how close nonresponders came to the thresholds.

It also shows why estimates, uncertainty, and analysis methods belong together. The sponsor reported odds ratios with confidence intervals, while the simple unadjusted recalculations produced somewhat different p-values for some comparisons. A single threshold-based label would conceal that distinction. The registry flags the discrepancy, and the sponsor’s own analysis takes precedence; at the same time, the registry does not give enough model detail to reproduce that analysis independently.

The dose-ranging structure raises a further issue: several dose comparisons were made against placebo. Without reported multiplicity handling or a testing hierarchy, the individual p-values cannot be assumed to represent a family-wise confirmatory analysis. The record also distinguishes registered enrollment from the population defined for the primary endpoint, highlighting why population definitions and missing-data handling matter.

For biostatisticians and clinical researchers, the central lesson is not a treatment recommendation. It is the value of evaluating the outcome definition, denominator, effect measure, uncertainty, model, missingness, and multiplicity together. These elements determine what a posted result can support and what remains unresolved.

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

The registry record leaves important analysis details unresolved. It names ANCOVA for the sponsor-reported odds ratios but does not describe the full model, covariates, or estimation procedure. The discrepancy flagged between those estimates and the summary-level unadjusted recalculations cannot be explained from the record. The sponsor’s own analysis takes precedence, but its reproducibility is limited by the level of methodological detail reported.

The primary endpoint population requires treatment receipt and baseline and postrandomization symptom ratings. The record does not provide a full account of participant flow into and out of this analysis population, nor a missing-data method or sensitivity analysis. Since diary completion is also built into the response definition, the handling of incomplete diaries could affect classification.

Four dose comparisons are reported, but multiplicity control, a prespecified testing hierarchy, and interim-analysis plans are not reported in the registry record. This limits interpretation of the individual p-values as a coordinated set of tests. The original sample-size justification and the trial’s own power assumptions are also not reported; the posted planning illustrations are not substitutes for those original design calculations.

The primary result is a composite assessed at Week 4. It does not provide separate component-level primary results or establish durability beyond the reported endpoint timeframe. The registry lists secondary outcomes but does not include their result values in this set of details. Safety summaries are descriptive, use group denominators that differ from some efficacy denominators, and do not report deaths. These limitations constrain what can be inferred from the registry summaries without implying that unreported analyses or outcomes were absent from other records.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy, Safety, and Tolerability of JNJ-27018966 (Eluxadoline) in the Treatment of Irritable Bowel Syndrome With Diarrhea — NCT01130272.
• Registry record last updated 2019-10-22; status last verified 2019-09.
• Results first posted 2019-10-22.
• 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

The registry describes a completed Phase 2 randomized, quadruple-masked, parallel-group, placebo-controlled dose-ranging study of eluxadoline in irritable bowel syndrome with diarrhea. Registered enrollment was 807. Eluxadoline doses of 5 mg, 25 mg, 100 mg, and 200 mg were compared with matching placebo, taken orally twice daily for up to 12 weeks.

The primary outcome was the percentage meeting a composite abdominal-pain and stool-consistency response definition at Week 4. Posted response percentages were 12.4%, 12.0%, 11.0%, and 13.8% for the four doses, compared with 5.7% for placebo. The registry reports sponsor ANCOVA odds ratios and confidence intervals, and flags a discrepancy with simple unadjusted recalculations; the sponsor’s analysis takes precedence.

The registry record does not report multiplicity handling, detailed missing-data methods, or the original sample-size justification. Safety summaries report serious and other adverse-event counts by group, but deaths are not reported in the registry record.