Study Comparing Rifaximin With Xifaxan 200 mg in Traveler's Diarrhea: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study Comparing Rifaximin With Xifaxan 200 mg in Traveler's Diarrhea (NCT02498418), a randomized phase 3 study. The primary outcome is Number of Participants Who Achieved Clinical Cure at Test of Cure (TOC) Visit (Within 24 to 72 Hours From the Time of Last Dose): Per-Protocol (PP) Population.

2. Clinical Question

The clinical-cure assessment was made at the test-of-cure visit, specified as Day 5, 6 or 7. The endpoint description also places the visit within 24 to 72 hours from the time of the last dose. The outcome was a binary participant-level classification: each participant was counted as having achieved clinical cure or not, under the registry’s stated symptom criteria.

The trial’s primary objective was to compare the clinical-cure rates for the test product, generic rifaximin, and the reference product, Xifaxan. This is distinct from asking whether either product differs from placebo. Although a placebo arm appears in the trial, it was not part of this primary endpoint’s bioequivalence evaluation. The primary comparison therefore concerns similarity between the two active-product groups, not a placebo-controlled estimate of treatment effect.

3. Trial Design

This was a randomized, triple-masked, parallel-design, multicenter phase 3 study. The registry lists 739 participants enrolled and the study status as completed. The recorded start date is 2016-01-06, and the primary completion date is 2017-02-28. The sponsor was Actavis Inc.

Participants were assigned to generic rifaximin 200 mg tablets, Xifaxan 200 mg tablets, or placebo. The two active-product regimens were oral dosing 3 times daily for 3 days; the placebo description also specifies dosing 3 times daily for 3 days. The registry identifies the study as randomized and triple-masked, but does not report which roles were masked or provide further details about the randomization procedure or allocation ratio.

The primary efficacy analysis compared the generic and reference product groups in the per-protocol population. The registry’s population description requires participants to have taken the 3-day study drug regimen, complied with dosing, completed the specified visit within 24–72 hours after the last dose, and had no major protocol deviations or violations that would affect treatment evaluation. The primary endpoint description also says that participants discontinued early for lack of treatment effect after completing 9 doses within 72 hours from the first dose were included in the per-protocol analysis using last observation carried forward. Participants whose condition worsened and required alternate or supplemental therapy were likewise discontinued and included using that method.

The trial record lists time to last unformed stool and microbiological cure at the test-of-cure visit as secondary outcomes. The primary endpoint was clinical cure at the test-of-cure visit. The registry lists four outcome measures and three analyses, but further details about other outcome measures are not reported in the registry record. The original sample-size justification, planned interim analyses, and fuller statistical 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: A total of 739 nonindigenous travelers with naturally acquired acute diarrhea were enrolled and randomized in this study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: PP population: randomized participants, met inclusion/exclusion criteria, took 3 days of study drug, were compliant with study drug dose, and completed Visit 3 within 24-72 hours from the time of last dose, with no major protocol deviations/violations that would affect treatment evaluation. LOCF method was used as applicable for this population.

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: Randomized population included all the participants who satisfied the inclusion and exclusion criteria and were randomized into the study.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Who Achieved Clinical Cure at Test of Cure (TOC) Visit (Within 24 to 72 Hours From the Time of Last Dose): Per-Protocol (PP) Population, measured over TOC visit (Day 5, 6 or 7).

The primary endpoint counted participants in the per-protocol population who achieved clinical cure at the test-of-cure visit, specified as Day 5, 6 or 7. The registry defines clinical cure using either of two symptom patterns: no stools or only formed stools over a 48-hour period with no fever, with or without other enteric symptoms; or no watery stools, or no more than 2 soft stools, over a 24-hour period with no fever and no other enteric symptoms apart from mild excess gas or flatulence.

This is a binary endpoint: each participant is classified as having achieved clinical cure or not. The registry reports the number of participants meeting the definition in each active-product group, alongside the per-protocol group sizes. The endpoint is used because the stated primary objective is clinical bioequivalence between generic rifaximin and Xifaxan with respect to clinical-cure rates. The placebo group was not included in this endpoint’s bioequivalence evaluation.

In general, a binary clinical endpoint makes the comparison interpretable as a difference in the proportion of participants meeting the stated outcome. Its meaning depends on how the outcome is defined, when it is assessed, and which participants are included. Here, the visit timing and symptom criteria are specified, but the registry does not report the equivalence margin or the full statistical method used for the sponsor’s equivalence analysis.

7. Results Posted in the Registry

• Xifaxan 200 mg Tablets: 51.4% (93/181) versus 49.5% (90/182) on control; risk difference 1.9 percentage points (95% CI -8.4 to 12.2), risk ratio 1.04 (0.85–1.27); unadjusted two-proportion z-test p = 0.713.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a count of participants meeting a binary clinical-cure definition. For a binary endpoint, a group’s observed cure rate is the number meeting the endpoint relative to the number analyzed. The posted counts are 90 of 182 for generic rifaximin and 93 of 181 for Xifaxan. The registry’s own analysis reports a difference in percentage of participants, while the unadjusted recalculation expresses the contrast as a risk difference. These are absolute-difference measures: they describe how far apart the two group proportions are, rather than comparing them as a ratio.

The recalculated risk difference is oriented as Xifaxan minus generic rifaximin and is 0.019. Its interval is -0.084 to 0.122, and its unadjusted p-value is 0.713. These are simple unadjusted recalculations from the posted summary statistics. They do not account for covariates or other features of an analysis model. The registry does not identify the method used for its reported equivalence analysis, so the recalculation should not be treated as a reproduction of that analysis.

In general, a confidence interval describes a range of values compatible with the data under the method used to construct it. It communicates uncertainty around an estimate; it is not a guarantee that the true value lies in the interval. The interval’s interpretation depends on its confidence level and statistical method. The sponsor’s reported interval is explicitly 90%, whereas the confidence level and method for the recalculated interval are not reported in the registry record. The numerical intervals therefore should not be treated as interchangeable estimates from the same procedure.

Equivalence testing is designed to assess whether a difference is small enough to fall within a defined range of acceptable differences. In general, an equivalence margin must be specified in advance, and the confidence interval is evaluated against that margin. The registry classifies its analysis as an equivalence analysis and reports the estimated difference and 90% interval, but the margin and the statistical method are not reported in the registry record. Without the margin, the reader cannot determine from the interval alone whether the sponsor’s prespecified equivalence criterion was met.

The reported unadjusted p-value tests a difference under the method used for the recalculation. In general, a p-value measures how compatible observed data are with a specified null hypothesis under the statistical model; it is not the probability that the null hypothesis is true. A p-value that does not indicate a clear difference does not, by itself, show that two products are equivalent. The equivalence objective requires its own criterion and analysis.

The endpoint is analyzed in a per-protocol population. This population is defined by completion and adherence conditions, as well as exclusion of major protocol deviations or violations that could affect treatment evaluation. Per-protocol analyses can be relevant to an equivalence question, but exclusions and adherence requirements affect which participants contribute to the estimate. The registry also states that some participants discontinued for lack of treatment effect or worsening condition and were included in the per-protocol analysis using last observation carried forward. In general, last observation carried forward substitutes an earlier recorded outcome for a later unavailable assessment. Such an approach relies on assumptions about what the unobserved outcome would have been; the registry does not provide further details about those assumptions or sensitivity analyses.

The primary comparison excludes placebo because the registry says placebo was not included in the bioequivalence endpoint evaluation. That choice aligns the reported endpoint comparison with the stated objective of comparing the test and reference products, but it means the primary cure counts do not estimate a contrast against placebo. The registry record does not provide details of any additional efficacy analyses that would change that interpretation.

Multiplicity arises when several outcomes, time points, groups, or statistical tests are assessed. In general, testing many questions can increase the chance of obtaining a seemingly notable result by chance, and prespecified strategies may address that issue. The registry lists two secondary outcomes, four outcome measures, and three analyses, but a multiplicity strategy is not reported in the registry record. The record also does not report whether interim analyses were planned or conducted. Those omissions limit assessment of how the full set of analyses was managed, but they do not change the arithmetic of the posted primary endpoint counts.

Finally, statistical precision and clinical interpretation are separate. The estimated difference and its interval describe uncertainty in the group contrast under a particular calculation. They do not specify what difference would be considered acceptable for bioequivalence. That judgment depends on the prespecified margin, which is not reported in the registry record.

10. Confidence Intervals and Precision

The posted counts yield a recalculated risk difference of 0.019 for Xifaxan minus generic rifaximin. The reported interval for that recalculation extends from -0.084 to 0.122. In general, an interval gives a range of values compatible with the data and method, illustrating that the point estimate is not known with certainty. This interval includes zero and also spans differences in either direction. It therefore does not isolate a single precise difference.

The registry’s sponsor analysis reports the difference in the opposite direction, -0.019, with a 90% confidence interval from -0.11 to 0.07. The sign reflects the reversed group order, not a conflicting direction of calculation. The two intervals come from different reporting contexts: the sponsor’s interval is identified as 90%, while the confidence level and method for the simple recalculation are not reported in the registry record. They should not be compared as if they were necessarily generated by the same procedure.

For an equivalence question, precision must be judged relative to a prespecified acceptable-difference margin. A narrow interval may support a stronger conclusion than a wide one, but whether it supports equivalence depends on where its limits fall relative to that margin. The equivalence margin is not reported in the registry record, so the sponsor’s interval cannot be judged against the trial’s stated criterion from these results alone.

The per-protocol group sizes were 182 and 181. The size and uncertainty of an estimate are related, but the observed interval is the relevant description of precision for this analysis. The registry does not report a confidence level for the recalculated interval, so its exact coverage interpretation should not be inferred.

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 illustrations are for participants per arm, not total events. They use the observed effect as a planning reference and show scenarios for detecting 100%, 75%, and 50% of that effect. The estimates are based on a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. For time-to-event outcomes, the stated convention would instead be total events, but the primary endpoint analyzed is binary and the listed figures are participants per arm.

The columns for 80% and 90% power describe different planning targets. In plain terms, a design with 80% power is intended to have an 80% chance of detecting the specified effect under the planning assumptions, while a design with 90% power is intended to have a 90% chance. The listed participants per arm rise as the target effect becomes smaller: the illustration requires more participants to detect 75% or 50% of the observed effect than to detect the full observed effect. The values are planning illustrations based on the observed effect, not the trial’s own original design assumptions, which are not reported in the registry record.

These figures are not observed power. They do not describe the probability that the completed trial detected an effect after the data were collected. Instead, they show how sample-size requirements vary under the stated assumptions and effect scenarios. The plotted planning curve presents the same general relationship visually; it should be read as an illustration, not as evidence about the trial’s actual power or design process.

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 = 0.495; treatment proportion p₁ = 0.514; average p̄ = 0.504.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7071 = 1.3859.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7070 = 0.5950.
4. n = (1.3859 + 0.5950)² / (0.0193)² = 10,526.5, rounded up to 10,527 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 <- 0.494505494505495                          # control proportion
p1 <- 0.513812154696133                          # 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(2498418)
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 = 10,527 (80% power), 14,092 (90% power)
 75% of observed effect: n per arm = 18,716 (80% power), 25,055 (90% power)
 50% of observed effect: n per arm = 42,113 (80% power), 56,377 (90% power)
power.prop.test: 10526.5 
Simulated power at n = 10,527 per arm: 0.798 (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 registry reports the sponsor’s own primary analysis as an equivalence analysis of the difference in percentage of participants. It gives a value of -0.019 and a 90% confidence interval from -0.11 to 0.07. The method and the equivalence margin are not reported in the registry record. Because the trial’s stated objective is clinical bioequivalence, this reported analysis is the result most directly aligned with that objective, but the missing margin prevents independent assessment of the equivalence criterion.

The simple recalculation uses the posted counts and expresses the risk difference in the reverse direction, Xifaxan minus generic rifaximin. It gives 0.019, an interval from -0.084 to 0.122, and an unadjusted p-value of 0.713. The sign difference between the two point estimates is consistent with reversing the group order. The recalculation is not the sponsor’s method and is not a substitute for the registry’s reported equivalence analysis.

The discrepancy flag is false, so the posted record does not identify a discrepancy between these results. The different intervals should still be understood in light of their stated contexts and potentially different methods. The recalculated p-value addresses a difference test, not the equivalence criterion. No conclusion about whether the sponsor’s margin-based criterion was met can be verified without the margin and fuller analysis details.

14. Multiplicity, Missing Data and Analysis Populations

The primary endpoint analysis uses a per-protocol population. The registry defines this as randomized participants who met the inclusion and exclusion criteria, took 3 days of study drug, complied with dosing, completed Visit 3 within 24–72 hours from the last dose, and had no major protocol deviations or violations that would affect treatment evaluation. This definition is important because the reported group sizes and cure counts apply to this analysis population, not necessarily to every enrolled participant.

The endpoint description includes two forms of early discontinuation in the per-protocol analysis using last observation carried forward. Participants who stopped early for lack of treatment effect after completing 9 doses within 72 hours of their first dose were included using that method. Participants whose condition worsened and required alternate or supplemental therapy were also discontinued and included using last observation carried forward. The registry does not report how many participants were handled this way, the specific substituted observations, or sensitivity analyses using alternative missing-data methods.

In general, missing-data methods require assumptions about outcomes that were not observed. Last observation carried forward uses an earlier observation in place of a later unavailable value. Its suitability depends on the setting and assumptions about how outcomes would have changed after the last measurement. The registry does not report those assumptions or further details about missing outcome data, so the robustness of the primary result to missing-data choices cannot be assessed from the record.

The registry lists two secondary outcomes: time to last unformed stool and the percentage of participants achieving microbiological cure at the test-of-cure visit within 24 to 72 hours from the last dose. It also lists four outcome measures and three analyses. A multiplicity adjustment or strategy for interpreting this set of analyses is not reported in the registry record. In general, multiplicity matters when several statistical questions are considered because it can affect the interpretation of nominal results. The record also does not report interim analyses or whether any were planned.

The original sample-size justification and the detailed statistical analysis plan are not reported in the registry record. The planning illustrations based on the observed effect are separate from those original design assumptions and should not be used to infer them.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures are reported for the safety groups, which are distinct from the per-protocol groups used for the primary clinical-cure endpoint. The registry lists 246 participants at risk in the generic rifaximin group, 247 in the Xifaxan group, and 244 in the placebo group. It reports 0 serious adverse events in each of these groups and 0 deaths in each group.

These are counts, not rates calculated for comparison. The registry also reports 17 other adverse events in each active-product group and 24 in the placebo group, using the stated at-risk groups. No serious adverse event terms are listed among the top serious terms. The record does not provide additional detail about event types, timing, severity beyond the serious/non-serious grouping, or statistical comparisons.

In general, a count of zero recorded serious events means none were reported in the listed group during the recorded period; it does not establish that an event is impossible or characterize risk outside the trial. The safety counts should be read descriptively, alongside their group denominators, and not as a substitute for the primary endpoint analysis.

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

The posted primary results show clinical-cure counts of 90 of 182 participants for generic rifaximin and 93 of 181 for Xifaxan in the per-protocol population. The sponsor’s registry analysis is labeled as an equivalence analysis and reports a difference of -0.019 with a 90% confidence interval from -0.11 to 0.07. A separate unadjusted recalculation reports a risk difference of 0.019 for Xifaxan minus generic rifaximin, with an interval from -0.084 to 0.122 and an unadjusted p-value of 0.713.

These statistics describe the observed clinical-cure comparison and its uncertainty. The recalculated p-value does not establish equivalence, and the group counts alone do not show that the products are identical. A formal equivalence interpretation depends on the prespecified margin and analysis. The margin is not reported in the registry record, so the equivalence criterion cannot be independently checked using the posted information.

The comparison is limited to the two active products in the per-protocol analysis. The placebo group was excluded from the primary bioequivalence endpoint, so the primary results do not estimate a difference between either active product and placebo. The findings also reflect the registry’s clinical-cure definition, test-of-cure timing, population rules, and stated use of last observation carried forward for specified early discontinuations.

The registry’s safety counts report no serious adverse events or deaths in any listed group, alongside counts of other adverse events. Those counts provide descriptive information for the recorded safety groups; they do not answer the primary equivalence question. The posted results do not resolve questions about outcomes not reported, unreported analysis details, or how results might differ under alternative missing-data assumptions.

17. Why This Trial Matters Statistically

This trial illustrates why an equivalence question should not be reduced to asking whether a conventional difference test is statistically notable. The primary objective was clinical bioequivalence between a generic product and a reference product. That objective calls for a margin-based interpretation, whereas the unadjusted recalculation’s p-value addresses a difference test. These approaches answer different statistical questions.

The endpoint also shows how a clinical outcome becomes an analysis variable. The registry defines clinical cure using symptom patterns over specified periods and assesses it at a specified test-of-cure visit. The reported counts then represent participants meeting that definition in the per-protocol population. The population rules and the approach to early discontinuation are part of the statistical meaning of the result, not incidental details.

The contrast between the sponsor’s reported equivalence analysis and a simple recalculation demonstrates the importance of preserving analysis context. The calculations use different orientations and are reported with different intervals; the method for the sponsor’s analysis and the equivalence margin are not reported. A straightforward reanalysis can help describe the posted counts, but it cannot replace missing protocol details or recreate an analysis whose method is unspecified.

Finally, planning illustrations based on the observed effect should not be mistaken for the trial’s original design rationale or for a measure of power after completion. They describe how sample size changes under explicit planning assumptions and effect scenarios. Keeping design planning, observed estimates, and inferential conclusions distinct is central to reading clinical trial results accurately.

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 does not report the equivalence margin, so the central criterion for interpreting the stated bioequivalence objective cannot be checked. It also does not report the method used for the sponsor’s equivalence analysis, the confidence level and method for the recalculated interval, or a detailed statistical analysis plan. The sponsor’s reported interval and the simple recalculation therefore should not be assumed to arise from identical procedures.

The primary endpoint analysis is per protocol, with eligibility and adherence conditions that narrow the analyzed population. The record describes last observation carried forward for specified early discontinuations but does not give the number of participants affected or sensitivity analyses under other missing-data approaches. The impact of those choices cannot be assessed from the posted details.

The primary bioequivalence comparison does not include the placebo group. The posted primary outcome therefore addresses the active-product comparison only. Although secondary outcomes are listed, the record does not report a multiplicity strategy, and details about the original sample-size justification, interim analyses, and full analysis plan are not reported in the registry record.

The registry identifies the trial as randomized, triple-masked, parallel-design, and multicenter, but does not report the randomization procedure, allocation ratio, or which roles were masked. The posted safety figures are counts and do not provide further detail about event timing or types. These limitations constrain interpretation of the record; they do not change the reported endpoint counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study Comparing Rifaximin With Xifaxan 200 mg in Traveler's Diarrhea — NCT02498418.
• Registry record last updated 2019-12-05; status last verified 2019-12.
• Results first posted 2019-12-05.
• 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

NCT02498418 is a completed randomized, triple-masked, parallel-design phase 3 study comparing generic rifaximin 200 mg tablets with Xifaxan 200 mg tablets, with a placebo group also included. The registry lists 739 participants enrolled. The primary objective was clinical bioequivalence based on clinical-cure rates at the test-of-cure visit.

In the per-protocol primary analysis, 90 of 182 participants in the generic rifaximin group and 93 of 181 in the Xifaxan group achieved clinical cure. The sponsor’s reported equivalence analysis gives a difference of -0.019 and a 90% confidence interval from -0.11 to 0.07. A simple unadjusted recalculation reports a risk difference of 0.019 for Xifaxan minus generic rifaximin, with an interval from -0.084 to 0.122 and an unadjusted p-value of 0.713.

The equivalence margin and full statistical methods are not reported in the registry record. The primary results should therefore be read as an endpoint comparison with uncertainty, not as an independently verifiable equivalence conclusion.