One Year Study of Rifaximin Delayed Release (DR) in Crohn's Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for One Year Study of Rifaximin Delayed Release (DR) in Crohn's Disease (NCT02240108), a randomized phase 3 study. The primary outcome is Number of Participants Who Achieved Clinical Symptom Remission (From CDAI Item 1) at Week 16.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, quadruple-masked, parallel-group study comparing rifaximin EIR with matching placebo in participants with active moderate Crohn’s disease. Its official title describes a double-blind, placebo-controlled, multicenter, multiregional study lasting one year. The two treatment descriptions specify oral dosing twice daily for 52 weeks. The rifaximin arm is titled “Rifaximin EIR 800 mg,” and its description specifies 400 mg tablets twice daily.

The primary objective was to assess induction of clinical remission and endoscopic response at 16 weeks. The primary outcome posted in the registry record is narrower: the number of participants meeting the CDAI Item 1 stool-frequency criterion for clinical symptom remission at Week 16. The study description also identifies clinical and endoscopic remission following an additional 36 weeks of treatment as a key secondary objective. The registry record lists three posted secondary outcomes, including a Week 16 clinical-remission outcome and Week 52 symptom and endoscopic outcomes.

Enrollment is listed as 81. The Week 16 primary endpoint results use denominators of 35 in the rifaximin arm and 45 in the placebo arm. The record does not explain how those endpoint denominators relate to total enrollment. The primary population is described as the intent-to-treat population, defined in the record as all randomized participants who received at least 1 dose of study drug. Further detail about exclusions or the handling of participants without endpoint data is not reported in the registry record.

The study began on 2014-10-28, and its primary completion date is listed as 2017-10-06. Its status is terminated. A reason for termination is not reported in the registry record. The trial’s original sample-size justification, planned interim analyses, and detailed statistical analysis plan are also not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Participants were randomized in a 1:1 allocation to Rifaximin EIR 800 mg or Placebo at the beginning of the treatment period and were maintained on that treatment assignment for 16 weeks, followed by an open-label long-term active treatment extension of an additional 36 weeks.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT population included all randomized participants who received at least 1 dose of 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: Intent-to-treat (ITT) population included all randomized participants who took at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Who Achieved Clinical Symptom Remission (From CDAI Item 1) at Week 16, measured over Week 16.

The primary endpoint counts participants meeting a symptom threshold based on CDAI Item 1 at Week 16. The threshold is no more than 10 liquid or very soft stools in the 7 days before the visit. This outcome reduces each participant’s stool-frequency information over that period to whether the threshold was met, then compares the number meeting it between treatment arms.

CDAI is described in the registry record as a weighted composite index covering stool frequency, abdominal-pain severity, general well-being, extraintestinal manifestations, antidiarrheal-agent use, abdominal mass, hematocrit, and body weight. Its scores range from 0 to approximately 600, with higher scores indicating greater disease severity. The primary endpoint does not use the overall CDAI score as its threshold: it uses stool frequency alone, from Item 1.

A symptom endpoint can address a participant-experienced feature of disease, while an endoscopic endpoint assesses a different aspect. The registry’s primary objective refers to both clinical remission and endoscopic response, but the posted primary outcome is the Item 1 symptom measure. The Week 16 CDAI score threshold for clinical remission is a separate secondary outcome. Keeping these definitions distinct matters when interpreting results: meeting the Item 1 threshold does not itself establish that a participant met the full-score remission definition or an endoscopic criterion.

General: a binary endpoint such as this records whether a defined condition was met, rather than the degree to which each participant’s symptom count changed. It is interpretable as a count or proportion meeting the criterion, but it does not convey the full distribution of stool counts or other CDAI components.

7. Results Posted in the Registry

• Rifaximin EIR 800 mg: 17.1% (6/35) versus 17.8% (8/45) on control; risk difference -0.6 percentage points (95% CI -17.4 to 16.1), risk ratio 0.96 (0.37–2.52); unadjusted two-proportion z-test p = 0.941.

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 Participants Who Achieved Clinical Remission (Defined as CDAI Score of <150) at Week 16

• 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:
  • Rifaximin EIR 800 mg: 48.6% (17/35) versus 26.7% (12/45) on control; risk difference 21.9 percentage points (95% CI 0.9 to 42.9), risk ratio 1.82 (1.01–3.29); unadjusted two-proportion z-test p = 0.043.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Rifaximin EIR 800 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants Who Achieved Clinical Symptom Remission (From CDAI Item 1 and 2 Both) Over Time

• 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:
  • Rifaximin EIR 800 mg: 5.7% (2/35) versus 6.7% (3/45) on control; risk difference -1.0 percentage points (95% CI -11.5 to 9.6), risk ratio 0.86 (0.15–4.85); unadjusted two-proportion z-test p = 0.861.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rifaximin EIR 800 mg and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With SES-CD Score of 0 at Week 52

• 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:
  • Rifaximin EIR 800 mg: 0.0% (0/35) versus 6.7% (3/45) on control; risk difference -6.7 percentage points (95% CI -14.0 to 0.6); unadjusted two-proportion z-test p = 0.119.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rifaximin EIR 800 mg and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover more than one construct and time point: full-score clinical remission at Week 16, a combined symptom-remission measure over time, and an endoscopic outcome at Week 52. Across this set, the directions are mixed rather than consistently favoring one arm. The Week 16 full-score remission comparison points in a different direction from the primary Item 1 symptom measure, while the later symptom and endoscopic results do not reinforce a consistent pattern of improvement across outcomes.

This variation is not necessarily a contradiction. The primary outcome uses a stool-frequency threshold, whereas the full-score remission outcome applies a CDAI score criterion, the combined symptom measure uses two CDAI items, and the endoscopic outcome uses SES-CD. Different definitions can classify participants differently, and outcomes assessed over different periods answer different questions. The primary result should therefore be interpreted as evidence about the specific Item 1 threshold at Week 16, not as a summary of every clinical or endoscopic outcome.

General: secondary outcomes can add context, explore whether findings extend to other measures, and help describe the breadth of results. Their evidential weight depends on whether they were prespecified, how many outcomes were tested, how missing data were handled, and whether statistical testing was adjusted or organized in a hierarchy. The registry record lists three posted secondary outcomes and no reported analyses; it does not report a multiplicity procedure or a detailed statistical analysis plan.

Because the secondary comparisons are unadjusted, a nominally notable result among several outcomes can be less persuasive than a single result specified as primary in advance. Conversely, a secondary result that is not notable does not by itself prove that no difference exists, particularly when precision is limited. The secondary findings are best treated as supportive or exploratory context. They neither change the definition of the primary endpoint nor resolve the uncertainty in its estimate.

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

• Number of Participants Who Achieved Clinical Remission (Defined as CDAI Score of <150) at Week 16
• Number of Participants Who Achieved Clinical Symptom Remission (From CDAI Item 1 and 2 Both) Over Time
• Number of Participants With SES-CD Score of 0 at Week 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the CDAI Item 1 stool-frequency threshold at Week 16 or did not. The registry reports counts and denominators for both arms, and the posted comparison expresses the contrast as a risk difference. The estimate is -0.006, defined in the posted comparison as the rifaximin proportion minus the placebo proportion. A negative estimate therefore means the observed proportion was lower in the rifaximin arm for this endpoint. The confidence interval and p-value are unadjusted.

What does a risk difference describe?

General: a risk difference subtracts the proportion with an event in one group from the proportion with an event in the other group. Here, the event is meeting the stated symptom-remission threshold. A value near zero means the observed proportions are close. The estimate alone does not express how uncertain the comparison is; the confidence interval supplies that information. The risk difference is an absolute contrast, so it can be read in the same units as the proportions rather than as a relative measure.

How should the p-value be read?

General: a p-value is calculated under a null model, usually one that assumes no difference between groups. It describes how unusual data at least as incompatible with that null model would be if the model and its assumptions held. It is not the probability that the null hypothesis is true, nor the probability that the result occurred by chance. The reported unadjusted p-value for the primary comparison is 0.941. It should be considered alongside the estimate and interval, not as a stand-alone measure of the size or importance of an effect.

What does the confidence interval add?

General: a confidence interval conveys the range of values compatible with the observed data under the method used to calculate it. Wider intervals indicate less precision. A 95% confidence interval is not a guarantee that the true value lies in the particular interval, and it does not resolve questions about bias, missing data, or the appropriateness of the analysis. The primary risk-difference interval extends from -0.174 to 0.161 and includes zero, as well as values on either side of zero. This is consistent with uncertainty about the direction and magnitude of the difference.

What is and is not documented?

The registry record lists no reported analyses for the secondary outcomes and no analyses in the analysis count. It does post the outcome counts and the unadjusted comparisons described in the results. The detailed statistical analysis plan, the original sample-size justification, the prespecified method for missing outcomes, and any interim analyses are not reported in the registry record. It is therefore not possible to determine from the record whether the posted analysis followed a more detailed prespecified plan or how any analysis choices were made.

General: randomization is intended to make treatment groups comparable on average at baseline, while masking is intended to reduce the influence of treatment knowledge on behavior or assessment. Those design features do not ensure that every source of bias is absent. Their practical protection can depend on implementation, adherence, follow-up, and analysis decisions; further information on those matters is not reported in the registry record.

The sample-size illustrations are calculated from the observed effect using a two-sided significance level of 0.05, equal allocation, and a normal approximation. They show planning requirements for stated fractions of the observed effect, not the original design calculation. General: sample-size planning depends on assumptions about the effect to detect, outcome frequency, significance level, power, allocation, and statistical method. The record supplies some assumptions for the posted illustration, but the original trial-specific rationale remains unreported.

For secondary outcomes, p-values are labeled unadjusted. General: when several outcomes are examined, the chance of at least one apparently notable result can increase if each is assessed without accounting for the others. Adjustment methods or a prespecified hierarchy can address multiplicity in different ways, but no such procedure is reported in the registry record. This matters especially when an isolated secondary comparison is interpreted alongside several outcomes and time points. The secondary findings should therefore be understood with greater caution than a single prespecified primary comparison.

11. Confidence Intervals and Precision

The primary estimate is a risk difference of -0.006. Its 95% confidence interval runs from -0.174 to 0.161. Because the interval includes zero, the posted data are compatible with no difference in the proportions meeting the threshold. The interval also extends to negative and positive differences, so the direction is not precisely determined by this estimate.

The interval’s breadth is important. It includes values corresponding to a meaningfully lower proportion in the rifaximin arm as well as a higher proportion, rather than concentrating tightly around the point estimate. The observed proportions, 0.171 and 0.178, are close, but the confidence interval indicates that the data do not pin down the underlying difference with comparable closeness. A small observed contrast is not, on its own, proof that the arms are equivalent.

General: confidence intervals are one way to express statistical precision. A narrow interval indicates that the estimate is relatively precise under its statistical assumptions; a broad interval indicates substantial uncertainty. An interval crossing zero does not mean the data prove there is no effect. It means the interval includes zero as a value compatible with the data under the method used. Likewise, a p-value above a conventional threshold does not demonstrate equivalence or establish that all relevant differences have been excluded.

The endpoint denominators are 35 for rifaximin and 45 for placebo. The registry record lists enrollment of 81, but does not explain the relation between enrollment and the endpoint denominators or provide enough detail to assess missing endpoint data. The uncertainty interval describes sampling variation under the calculation; it does not account for possible bias caused by missing data, deviations from the intended analysis, or other unreported features. The original analysis methods and missing-data strategy are not reported in the registry record, so precision should be interpreted as applying to the posted comparison rather than as resolving those additional uncertainties.

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 figures are planning illustrations based on the observed effect, not a report of the trial’s original design justification. For these binary outcomes, the figures are participants per arm, rather than a combined total across both arms or a total number of events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect.

The 80% power column gives the modeled number of participants per arm for a design with an 80% chance of detecting the assumed effect under the planning assumptions, if that effect and the other assumptions are correct. The 90% power column gives the corresponding number per arm for a design with a 90% chance. Power is a design property under assumed conditions; it is not a measure of whether the observed trial result is true or false. These figures are not observed power.

The rows compare planning for the full observed effect with planning for 75% and 50% of that effect. A smaller assumed effect requires more participants to distinguish it from no difference at the same significance level and power target. The listed figures can therefore rise sharply as the target effect becomes smaller. This is a feature of the planning calculation, not evidence that those participant counts were enrolled or that the original study used those assumptions.

The registry record does not report the trial’s own sample-size justification or original design assumptions. The planning illustration also does not establish whether the enrolled sample was adequate for the intended primary objective. It should be read as a conditional illustration of how sample requirements change under the specified assumptions, not as an explanation of the study’s enrollment or termination.

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 = 0.178; treatment proportion p₁ = 0.171; average p̄ = 0.175.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5369 = 1.0523.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5369 = 0.4518.
4. n = (1.0523 + 0.4518)² / (-0.0063)² = 56,118.3, rounded up to 56,119 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 <- 0.177777777777778                          # control proportion
p1 <- 0.171428571428571                          # 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(2240108)
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 = 56,119 (80% power), 75,126 (90% power)
 75% of observed effect: n per arm = 100,124 (80% power), 134,038 (90% power)
 50% of observed effect: n per arm = 226,082 (80% power), 302,659 (90% power)
power.prop.test: 56118.3 
Simulated power at n = 56,119 per arm: 0.799 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists three secondary outcomes in addition to the primary outcome, but does not report a plan for controlling multiplicity across those outcomes, time points, or comparisons. The posted secondary comparisons are unadjusted. It is also not reported in the registry record whether a formal testing hierarchy was specified or whether outcomes were designated as confirmatory versus exploratory.

General: testing multiple outcomes without adjustment can increase the chance that at least one comparison appears notable even when there is no underlying difference for any outcome. Adjustment procedures, gatekeeping, or a prespecified hierarchy can address this issue, but they may affect how results are interpreted. Without a reported procedure, secondary p-values should not be treated as though each were the only statistical test conducted. The primary endpoint remains the clearest single result for the stated primary comparison, while secondary findings provide context with additional uncertainty.

The registry record describes the primary population as all randomized participants who received at least 1 dose of study drug. It does not report an endpoint-specific missing-data strategy, the number of participants with missing Week 16 data, reasons for missingness, or any sensitivity analyses. Enrollment is listed as 81, while the primary endpoint denominators are 35 and 45. The record does not explain this relationship, so it is not possible to determine from the registry entry whether the discrepancy reflects endpoint availability, other analysis-population details, or another reason.

The original statistical analysis plan, the trial’s sample-size justification, and whether interim analyses were planned or conducted are not reported in the registry record. The record does not provide enough information to assess whether outcome definitions or analysis choices changed during the study. The study status is terminated, but the reason for termination is not reported. These gaps limit assessment of the analysis process and of how fully the posted results represent the intended study procedures.

15. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: crohn's disease (6.7%), vomiting (4.4%), anaemia (2.9%), coronary artery disease (2.9%), myocardial infarction (2.9%).

The serious adverse event counts are reported for 35 participants at risk in the rifaximin arm and 45 in the placebo arm. The record lists 6 participants with serious adverse events in the rifaximin group and 9 in the placebo group. It lists 25 participants with other adverse events in each group. No deaths are listed in either group.

The registry also lists serious-event terms with percentages: Crohn’s disease, 6.7%; vomiting, 4.4%; anaemia, 2.9%; coronary artery disease, 2.9%; myocardial infarction, 2.9%; and fatigue, 2.9%. These are terms reported in the serious-event listing; the record does not provide enough detail to infer whether any events were judged related to study treatment. The listed figures describe reported events and affected participants, not a causal comparison.

General: safety counts are descriptive. Differences in counts do not by themselves establish that an intervention caused an event or that risks differ between groups. Interpretation also depends on exposure, event definitions, follow-up, seriousness criteria, and completeness of reporting. Detailed safety-analysis methods and further context about event attribution are not reported in the registry record.

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

The posted primary result describes the proportion meeting one specific symptom threshold at Week 16. The observed proportions are close, and the unadjusted risk difference is close to zero. However, the confidence interval is broad and includes values in both directions. The data therefore do not precisely determine the underlying difference between arms for this endpoint.

This finding is not a test of every objective named in the study description. It does not, by itself, answer whether participants met full CDAI remission, whether endoscopic response occurred, or whether outcomes differed by Week 52. Those questions use separate endpoints and time frames. The secondary outcomes have mixed directions, and the registry record does not report a multiplicity procedure, so they should not be combined into a single claim of a consistent effect.

General: absence of strong evidence against a no-difference model is not the same as evidence that two treatments are equivalent. Equivalence or noninferiority requires an appropriate design and prespecified margin, neither of which is reported in the registry record. Similarly, a confidence interval that includes zero does not establish that all potentially important differences are excluded.

The posted comparison is unadjusted, and the registry record does not describe missing-data handling or the original analysis plan. The listed enrollment and endpoint denominators are not reconciled. These limitations mean that the statistical result should be read as a description of the posted comparison, with uncertainty about the extent to which it captures the full intended analysis.

The study is marked terminated, but the reason is not reported in the registry record. Termination status alone does not explain the endpoint results, establish that the trial stopped because of efficacy or safety, or indicate what would have happened under continued follow-up. The posted data support a cautious description of the measured outcomes and their precision; they do not warrant a broader conclusion beyond those data.

17. Why This Trial Matters Statistically

This study illustrates why endpoint definitions matter. Its primary objective refers to clinical remission and endoscopic response, but the posted primary outcome counts participants meeting a stool-frequency threshold from CDAI Item 1. That is a narrower measure than full CDAI remission and differs from the endoscopic outcomes. Readers need to distinguish the objective’s broad wording from the specific outcome used for the primary comparison.

It also illustrates the difference between a point estimate and its precision. The observed arm proportions are close and the estimated risk difference is near zero, yet the confidence interval spans values in both directions. A small estimate is not enough to conclude that the groups are equivalent; uncertainty must be considered alongside the estimate.

The secondary results demonstrate why a collection of outcomes should not be read as one unified test. The posted outcomes use different definitions and time points, and their directions are mixed. Because no multiplicity procedure is reported, isolated secondary findings deserve caution. The record’s missing detail about analysis plans and endpoint denominators further shows why registry results need to be read in the context of what is and is not documented.

Finally, the sample-size illustrations are conditional planning calculations based on observed effects, not the trial’s original justification or a measure of observed power. They show how assumptions about the effect to detect can change required enrollment. Keeping design planning, observed estimates, uncertainty, and trial conduct distinct is essential when interpreting a small clinical study 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 registry record provides limited information for evaluating how the trial was conducted and analyzed. Although enrollment is listed as 81, the primary endpoint denominators are 35 and 45, and the record does not explain the difference. It describes the primary population as randomized participants who received at least 1 dose, but does not report the number of participants missing the Week 16 outcome, reasons for missing data, or methods used to address missingness.

The primary outcome measures a single symptom criterion based on CDAI Item 1. It does not capture all components of the CDAI, and it is distinct from full-score remission and endoscopic outcomes. The posted secondary endpoints broaden the clinical picture, but their directions are mixed and they are unadjusted. The registry record does not report a multiplicity strategy, a testing hierarchy, or a detailed statistical analysis plan.

The posted primary comparison is unadjusted. The original sample-size justification and any planned interim analyses are not reported in the registry record. Consequently, the planning illustrations based on the observed effect cannot establish what sample size the investigators originally intended or whether enrollment met that original target. The figures should not be treated as evidence of observed power.

The study’s status is terminated, but the reason for termination is not reported in the registry record. The safety listing gives counts and selected event terms, but does not report enough detail to infer treatment attribution. The record also does not provide further information about adherence, treatment exposure, or the handling of protocol deviations. These omissions constrain interpretation of both the efficacy comparison and the safety counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: One Year Study of Rifaximin Delayed Release (DR) in Crohn's Disease — NCT02240108.
• Registry record last updated 2019-09-10; status last verified 2019-09.
• Results first posted 2019-09-10.
• 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

NCT02240108 is a Phase 3 randomized, quadruple-masked, parallel-group study of rifaximin EIR versus matching placebo in active moderate Crohn’s disease. The primary outcome is the number of participants meeting a CDAI Item 1 stool-frequency threshold at Week 16. The posted risk difference is -0.006, with a 95% confidence interval from -0.174 to 0.161 and an unadjusted p-value of 0.941.

The registry record lists enrollment of 81, a primary completion date of 2017-10-06, and status terminated. It posts three secondary outcomes with mixed directions. The original sample-size justification, detailed analysis plan, missing-data strategy, multiplicity procedure, and reason for termination are not reported in the registry record. The primary estimate should be read with its broad uncertainty and with the stated limits of the available record.