Study to Evaluate the Efficacy and Safety of Vibegron Administered Orally for 12 Weeks to Women With Irritable Bowel Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate the Efficacy and Safety of Vibegron Administered Orally for 12 Weeks to Women With Irritable Bowel Syndrome (NCT03806127), a randomized phase 2 study. The primary outcome is Number of Irritable Bowel Syndrome (IBS) With Predominantly Diarrhea (IBS-D) Participants Who Were Abdominal Pain Intensity (API) Weekly Responders at Week 12.

2. Clinical Question

The primary question is about a repeated weekly response criterion summarized at Week 12, rather than a single pain score on the final day. The endpoint counts participants who met that criterion; it does not describe the size of improvement among responders or the average change for all participants. The registry record describes the broader study as evaluating pain associated with IBS-D or IBS-M, but the posted primary endpoint is specifically for IBS-D. The registry record does not report a primary endpoint result for the IBS-M group.

3. Trial Design

This was a phase 2, randomized, triple-masked, parallel-group, placebo-controlled study of oral vibegron. The planned treatment period described in the registry record was 12 weeks. Participants were assigned to vibegron 75 mg once daily or matching placebo once daily. The record lists an enrollment of 222 and the study status as completed.

The study start date was 2018-12-31, and the primary completion date was 2020-09-25. The record identifies Urovant Sciences GmbH as sponsor. It does not report which specific roles were covered by triple masking, how randomization was generated or implemented, or whether allocation was stratified.

The primary analysis population was not all enrolled participants. It was the IBS-D Full Analysis Set, defined in the registry record as randomized IBS-D participants who took at least one dose of double-blind study medication and had at least one evaluable post-randomization weekly abdominal-pain score. The primary outcome lists 63 participants in the placebo arm and 66 in the vibegron arm. Those outcome denominators differ from the 111 participants at risk in each arm in the posted safety results; the record does not explain the relationship between these populations or give reasons for the difference.

The primary endpoint was a binary participant count: each participant either met the weekly responder definition or did not. The registry also lists secondary outcomes covering Global Improvement Scale responders, additional abdominal-pain response thresholds in IBS-D, treatment-emergent adverse events, laboratory values, and vital signs. Specific numerical results for every listed secondary outcome are not present in the record summarized by the posted results.

The registry record does not report the trial’s original sample-size justification, detailed randomization procedures, or planned interim analyses. Those design details should not be inferred from the study being randomized, masked, or completed.

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: Of 806 participants screened for this study, 222 were randomized (after a 2-week, single-blind placebo Run-in Period), and 222 received 1 dose of double-blind study drug in the Treatment Period (Safety Set: placebo, N = 111; vibegron, N = 111).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set for IBS-D participants: all randomized participants with IBS-D who who took at least one dose of double-blind study medication and had at least one evaluable post-randomization weekly API score (i.e., where evaluable was considered a minimum of 5 diary entries in a week)

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: Baseline data are reported for all randomized participants who took at least one dose of double-blind study medication and had at least one evaluable post-randomization weekly abdominal pain intensity (API) score (i.e., where evaluable was considered a minimum of 5 diary entries in a week).

6. Primary Endpoint

The registry lists the primary outcome as Number of Irritable Bowel Syndrome (IBS) With Predominantly Diarrhea (IBS-D) Participants Who Were Abdominal Pain Intensity (API) Weekly Responders at Week 12, measured over Baseline; Week 12.

The primary endpoint counts IBS-D participants who achieved a sustained weekly abdominal-pain response through the 12-week assessment period. The response definition required at least a 30% decrease from baseline in the weekly average of the worst abdominal-pain score recorded for the past 24 hours. A participant had to satisfy the criterion in at least 50% of assessed weeks from Week 1 to Week 12, corresponding to at least 6 weeks. A week counted as evaluable when the participant had at least 5 diary entries.

This endpoint is useful for describing whether participants crossed a prespecified threshold repeatedly over the treatment period. It gives a clinically interpretable responder count, rather than only an average that could be influenced by a small number of large individual changes. At the same time, it reduces a participant’s experience to a yes-or-no classification: it does not show how much pain changed beyond the threshold, which weeks were missed, or the pattern of scores among people who did not qualify as responders.

The endpoint is limited to the IBS-D analysis population, even though the study included women with IBS-D or IBS-M. It therefore does not directly summarize response for the full mixed-subtype study population. The registry record does not report the full distribution of weekly pain scores or the handling of missing diary weeks.

7. Results Posted in the Registry

• Vibegron 75 mg: 40.9% (27/66) versus 42.9% (27/63) on control; risk difference -1.9 percentage points (95% CI -19.0 to 15.1), risk ratio 0.95 (0.64–1.43); unadjusted two-proportion z-test p = 0.823.

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.

Number of IBS-D Participants Who Were API Weekly Responders With ≥ 40% Improvement Over 12 Weeks

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Vibegron 75 mg: 33.3% (22/66) versus 31.7% (20/63) on control; risk difference 1.6 percentage points (95% CI -14.6 to 17.8), risk ratio 1.05 (0.64–1.73); unadjusted two-proportion z-test p = 0.847.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vibegron 75 mg and the control. The interval gives the range of effects that remain compatible with the data.

Number of IBS-D Participants Who Were API Weekly Responders With ≥ 50% Improvement Over 12 Weeks

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Vibegron 75 mg: 27.3% (18/66) versus 20.6% (13/63) on control; risk difference 6.6 percentage points (95% CI -8.0 to 21.3), risk ratio 1.32 (0.71–2.47); unadjusted two-proportion z-test p = 0.378.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Vibegron 75 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover additional responder thresholds for abdominal pain in IBS-D, global improvement among IBS participants, and safety-related measures including treatment-emergent adverse events, laboratory values, and vital signs. The detailed numerical comparisons available for the two additional IBS-D abdominal-pain thresholds point in different ways in their point estimates: one is close to zero, while the other is positive for vibegron relative to placebo. Their intervals are broad and include zero. That overall pattern does not provide a consistently precise secondary signal that would resolve the uncertainty in the primary result.

These outcomes are related to, but not interchangeable with, the primary endpoint. They use alternative improvement thresholds, while the primary definition combines a 30% threshold with a requirement to meet it across multiple assessed weeks. A different threshold can change who qualifies as a responder. The secondary outcomes also include a broader IBS population for the Global Improvement Scale, while the primary endpoint is restricted to IBS-D.

The registry record lists six secondary outcomes, but it does not provide numerical results for every listed measure in the posted results. No unreported secondary result should be inferred from the primary result or from the entries that are available.

As a general statistical concern, examining several outcomes increases the chance that at least one result may appear notable by chance. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Accordingly, unadjusted secondary comparisons carry less weight than a prespecified primary analysis and should be treated as exploratory context rather than as independent confirmation. They do not erase the uncertainty in the primary estimate.

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

• Number of Global Improvement Scale (GIS) Responders at Week 12 for All IBS Participants, Including IBS-D and IBS-M Participants
• Number of IBS-D Participants Who Were API Weekly Responders With ≥ 40% Improvement Over 12 Weeks
• Number of IBS-D Participants Who Were API Weekly Responders With ≥ 50% Improvement Over 12 Weeks
• Number of Participants With Any Treatment-emergent Adverse Event (TEAE)
• Number of Participants With Clinically Meaningful Changes From Baseline in Clinical Laboratory Values at Week 12
• Number of Participants With Clinically Relevant Changes From Baseline in Vital Sign Values at Week 12

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: participants either met the responder definition or did not. For a binary outcome, the event count and the number of participants assessed in each group are the basic information. The primary results report 27 responders among 63 placebo participants and 27 among 66 vibegron participants. The corresponding posted proportions are 0.429 and 0.409.

What does a risk difference describe?

As a general statistical concept, a risk difference subtracts the event proportion in one group from the event proportion in the other. It is expressed on an absolute scale, so it describes the difference in the probability of the event rather than a relative multiplier. In the posted unadjusted recalculation, the risk difference is -0.019. The negative sign indicates that the estimated responder proportion is lower in the vibegron group than in the placebo group. The estimate is not a count of participants and should not be read as one.

How should the interval be read?

In general, a confidence interval describes uncertainty in an estimate under the method used to calculate it. A wider interval indicates less precision, while an interval that includes zero for a difference is compatible with no group difference as well as with differences in either direction. The recalculated interval runs from -0.190 to 0.151. The registry result reports a separate 90% confidence interval for the sponsor analysis; the confidence level for the recalculated interval is not reported in the registry record. A confidence interval is not a range in which each individual participant’s outcome lies, and it does not assign a probability that the true effect is at a particular point within the interval.

What does the p-value add?

As a general explanation, a p-value measures how unusual data at least as discrepant as those observed would be under a specified statistical model, often one that assumes no group difference. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The unadjusted p-value for the primary recalculation is 0.823. This value should be considered alongside the estimate and its interval rather than used alone to make a conclusion. A large p-value does not prove that the groups are equivalent.

What is the sponsor-reported method?

The registry reports a Cochran-Mantel-Haenszel difference for the primary result. In general, the Cochran-Mantel-Haenszel approach can estimate an association or treatment contrast across strata, accounting for the stratification used in an analysis. The registry record does not identify the strata or provide other implementation details. The sponsor’s reported difference is -1.9, and its 90% confidence interval is -16.1 to 12.3. The registry does not list a p-value for this reported analysis.

The recalculation uses posted arm-level counts to make a simple unadjusted comparison. It does not reproduce an analysis that might account for stratification or other prespecified features. The recalculation is therefore a supplementary way to read the arm-level data, not a replacement for the sponsor’s reported analysis. The record does not state whether the sponsor’s analysis adjusted for additional covariates.

Why does the binary threshold matter?

Responder analyses can be easy to communicate because they identify the proportion meeting a defined threshold. However, any threshold divides people with outcomes near the boundary into different categories, even if their underlying scores are similar. The primary definition also requires response in multiple weeks, which captures persistence but depends on weekly diary data and the rule for an evaluable week. The registry record specifies the minimum diary entries needed for an evaluable week, but does not report all procedures for handling unavailable or incomplete diary data.

Over-dispersion is a general concern for count outcomes when the observed variability exceeds the variability assumed by a statistical model. It is not a central feature of this primary endpoint, which is a participant-level binary response, rather than a rate or an unbounded event count. For binary outcomes, interpretation instead depends on the event definition, group denominators, analysis population, and method used to estimate the group contrast.

11. Confidence Intervals and Precision

The primary point estimate is an unadjusted risk difference of -0.019. Its posted interval extends from -0.190 to 0.151. Because the interval includes zero and spans values on both sides of zero, the estimate is not precise enough to determine the direction of the underlying group difference from these data alone. It also allows a range of possible effect magnitudes, rather than concentrating tightly around the point estimate.

The sponsor’s reported analysis has a 90% confidence interval from -16.1 to 12.3 around a CMH difference of -1.9. This interval also includes zero and allows differences in either direction. The recalculated interval and the sponsor’s interval come from different analyses and should not be treated as interchangeable: the recalculation is unadjusted, and details of the sponsor’s strata and implementation are not reported in the registry record.

As a general explanation, an interval’s width reflects both the observed data and the statistical method used. More information can make estimates more precise, but the interval also depends on the endpoint definition and analysis assumptions. The primary analysis includes 63 placebo participants and 66 vibegron participants, so the endpoint estimate is based on a subset of the total enrollment. The record does not report a confidence level for the recalculated interval, so none should be inferred from its endpoints.

Precision is distinct from whether a result crosses a conventional significance threshold. The point estimate alone does not convey how uncertain it is, and the p-value alone does not show the range of effects compatible with the data. Reading the estimate, interval, and analysis population together gives a more complete account of what the posted primary result can support.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations report participants per arm for the binary outcomes in this study, not total events. They use the observed effect as a starting point and show illustrations for detecting 100%, 75%, or 50% of that observed effect. For example, the primary-outcome planning figures list 10,068 participants per arm for 80% power and 13,478 participants per arm for 90% power when planning for 100% of the observed effect. The other effect fractions are listed alongside those values in the planning results.

The stated assumptions for these illustrations 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. These are planning assumptions for an illustration based on the observed effect; the trial’s own original sample-size assumptions and justification are not reported in the registry record.

In plain terms, the 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under its assumptions. The 90% power column uses a higher target chance of detecting that effect and therefore requires more participants in the listed scenarios. Planning for a smaller effect requires more participants, because a smaller group difference is harder to distinguish from random variation.

These are prospective planning illustrations, not evidence about the power achieved by the completed trial. They are not observed power.

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

Worked calculation for this trial

1. Control proportion p₀ = 0.429; treatment proportion p₁ = 0.409; average p̄ = 0.419.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6977 = 1.3675.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6976 = 0.5871.
4. n = (1.3675 + 0.5871)² / (-0.0195)² = 10,067.6, rounded up to 10,068 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 <- 0.428571428571429                          # control proportion
p1 <- 0.409090909090909                          # 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(3806127)
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 = 10,068 (80% power), 13,478 (90% power)
 75% of observed effect: n per arm = 17,928 (80% power), 24,000 (90% power)
 50% of observed effect: n per arm = 40,401 (80% power), 54,085 (90% power)
power.prop.test: 10067.6 
Simulated power at n = 10,068 per arm: 0.802 (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.

14. Analyses Reported by the Sponsor

The registry’s sponsor-reported primary analysis is a Cochran-Mantel-Haenszel difference of -1.9, with a 90% confidence interval from -16.1 to 12.3. No p-value is listed for that analysis. The interval includes zero and allows values on both sides, so the reported estimate is uncertain in direction and magnitude.

The unadjusted recalculation from the posted counts gives a risk difference of -0.019, with an interval from -0.190 to 0.151 and an unadjusted p-value of 0.823. This calculation uses the arm-level responder counts and denominators and does not reproduce the sponsor’s CMH method. The record does not report the strata or other implementation details for the sponsor analysis.

The estimates use different methods and are expressed in the units used by their respective analyses. They should be read as related summaries of the same primary outcome, not as if one were a correction of the other. The sponsor’s result is the analysis reported in the registry; the unadjusted result is an additional calculation from the posted counts. The registry record does not report further details about prespecified adjustment variables or the rationale for the sponsor’s method.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report a multiplicity-control plan for the primary and secondary outcomes, or an order in which secondary hypotheses were to be tested. This matters because evaluating multiple outcomes can raise the chance of a chance-positive finding across the set. Without a reported plan, the secondary comparisons should be interpreted cautiously and not as if each were the only test conducted.

The record also does not report the detailed handling of missing data for the primary endpoint. It defines an evaluable week as requiring at least 5 diary entries and defines the Full Analysis Set as randomized IBS-D participants who received at least one dose and had at least one evaluable post-randomization weekly API score. It does not explain how missing weeks or participants without post-randomization scores were treated in the analysis, whether any imputation was used, or how sensitivity analyses addressed missingness.

The stated analysis population is important: the primary estimate does not include every person enrolled in the study. The record lists 63 placebo and 66 vibegron participants in the primary outcome, while the safety results list 111 at risk in each group. The registry record does not explain the population difference, and it does not report a participant flow accounting for all exclusions from the primary analysis.

The registry gives a sponsor-reported CMH analysis but does not report the strata or the full statistical analysis plan. It also does not report whether interim analyses were planned or conducted, or the original sample-size justification. These omissions limit assessment of how fully the posted analysis follows the original plan. They do not establish that any particular procedure was or was not used; the relevant details are simply not reported in the registry record.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: covid-19 (0.9%), ectopic pregnancy (0.9%), hyperkalaemia (0.9%).

The safety results list 111 participants at risk in each group. Serious adverse events affected 1 participant in the placebo group and 2 in the vibegron 75 mg group. The registry reports no deaths in either group. The listed serious-event terms are COVID-19, ectopic pregnancy, and hyperkalaemia, each reported as 0.9%. The record does not assign these listed terms to a particular treatment group in the information summarized by the posted results.

These figures are descriptive counts. They do not, on their own, establish whether an event was caused by study treatment or whether a difference between groups is meaningful. Serious events are uncommon in the posted counts, so a small number of participants can have a substantial influence on the apparent group pattern. The record also reports other treatment-emergent adverse events in 19 placebo participants and 13 vibegron participants, but those counts are not a substitute for the serious-event summary.

As with the efficacy endpoint, the safety denominators are distinct from the primary analysis denominators. The registry record does not provide further detail about event adjudication or the relationship between the listed serious-event terms and the group-specific counts.

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

The posted primary data show that 27 participants in each group met the IBS-D weekly abdominal-pain responder definition. Because the arm denominators differ, the corresponding proportions are not identical: 0.429 for placebo and 0.409 for vibegron. The unadjusted risk-difference estimate is -0.019, with a broad interval that includes zero. The sponsor-reported estimate also has a 90% confidence interval that crosses zero.

These results do not provide a precise estimate of the direction or size of the primary group difference. They also do not prove that the treatments are equivalent or that there is no effect. Such claims would require a design and analysis specifically intended to assess equivalence or non-inferiority; the registry record does not report such a framework.

The endpoint captures a particular kind of response: a decrease of at least 30% in weekly average worst abdominal pain, sustained for at least 6 assessed weeks in the 12-week period. It does not describe all aspects of IBS symptoms, the magnitude of improvement beyond the threshold, or outcomes for participants with IBS-M. The registry record lists other secondary outcomes, but does not provide numerical results for every one.

Safety counts are also descriptive. The reported serious adverse events and absence of deaths in the posted safety results are not enough, by themselves, to determine cause or characterize rare risks. The record’s results should be read within the study population, treatment period, endpoint definitions, and analysis populations actually reported. They do not settle what would occur in other populations, over other durations, or under different treatment conditions.

In general, a trial estimate is one piece of evidence whose meaning depends on precision, design, analysis, and completeness of reporting. Here, the uncertainty around the primary comparison is substantial, and several analysis details are not reported in the registry record. The appropriate statistical reading is therefore descriptive and bounded by those limitations, rather than a broad claim about treatment effects.

18. Why This Trial Matters Statistically

This trial illustrates why a responder count should be read together with its definition, denominator, and uncertainty. The primary endpoint is not simply whether pain improved at any point: response required a prespecified decrease in weekly average worst abdominal pain and that decrease had to persist for a minimum number of assessed weeks. That design choice affects the meaning of the count and the participants classified as responders.

It also shows the distinction between an arm-level count and a comparative estimate. The same number of responders in each group does not by itself mean identical response proportions when the denominators differ. A risk difference expresses the comparison on an absolute scale, while its interval indicates how uncertain that estimate remains. The reported primary interval includes zero and spans values in both directions, so the point estimate should not be read in isolation.

The sponsor’s CMH result and the unadjusted recalculation provide different analytical summaries. Keeping those methods distinct is important: a simple comparison of posted counts does not reconstruct an analysis that may account for strata. At the same time, missing details about the sponsor method, missing-data handling, multiplicity, and original sample-size rationale limit a complete assessment of the analysis plan.

Finally, the registry’s planning illustrations demonstrate how sample-size requirements depend on the effect an investigator aims to detect and the desired power. Those calculations are not the trial’s original design justification and do not describe power observed after the study. Separating planning assumptions from trial results helps prevent a common misreading of retrospective sample-size calculations.

19. Limitations

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

The primary result applies to IBS-D participants meeting the defined Full Analysis Set criteria, not to all enrolled women or to the IBS-M subgroup. Although the study description includes IBS-D and IBS-M, the posted primary endpoint is restricted to IBS-D, and a numerical primary result for IBS-M is not reported in the registry record.

The endpoint depends on daily diary completion and a weekly evaluability rule requiring at least 5 entries. The registry record does not report how missing diary entries or nonevaluable weeks were handled, nor does it provide sensitivity analyses for missing data. The primary outcome denominators are also smaller than the safety at-risk counts, and the record does not account for the difference.

The primary comparison is based on 63 placebo participants and 66 vibegron participants. The interval is broad, and the sponsor’s reported analysis does not include a listed p-value. The details of the CMH strata and other implementation choices are not reported. The original sample-size justification and multiplicity plan are also not reported, limiting assessment of whether the study was designed to detect a particular clinically relevant effect or how secondary testing was controlled.

The treatment period described is 12 weeks, and the tested vibegron regimen is 75 mg orally once daily. The posted findings therefore concern this duration and regimen. The registry record does not support extrapolation to different doses, longer treatment, other populations, or outcomes not reported. The study is identified as phase 2, and the limitations of the registry’s outcome reporting should be kept in view when interpreting both efficacy and safety results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate the Efficacy and Safety of Vibegron Administered Orally for 12 Weeks to Women With Irritable Bowel Syndrome — NCT03806127.
• Registry record last updated 2021-08-02; status last verified 2021-07.
• Results first posted 2021-07-30.
• 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.

23. Record Summary

NCT03806127 is a completed phase 2 randomized, triple-masked, parallel-group, placebo-controlled study sponsored by Urovant Sciences GmbH. It enrolled 222 women with irritable bowel syndrome, including IBS-D and IBS-M, and compared oral vibegron 75 mg once daily with matching placebo for 12 weeks. The study began on 2018-12-31, and primary completion was recorded as 2020-09-25.

The primary endpoint counted IBS-D participants meeting a repeated weekly abdominal-pain response definition. The posted counts were 27 of 63 for placebo and 27 of 66 for vibegron. The unadjusted risk difference was -0.019, with an interval from -0.190 to 0.151 and p = 0.823. The sponsor-reported CMH difference was -1.9, with a 90% confidence interval from -16.1 to 12.3.

Secondary outcomes addressed additional symptom response and safety. The record reports serious adverse events affecting 1 placebo participant and 2 vibegron participants, with no deaths in either group. Important analysis details, including multiplicity procedures and missing-data handling, are not reported in the registry record.