The Safety/Efficacy of Rifaximin With/Without Lactulose in Participants With A History of Recurrent Hepatic Encephalopathy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Safety/Efficacy of Rifaximin With/Without Lactulose in Participants With A History of Recurrent Hepatic Encephalopathy (NCT01842581), a randomized phase 4 study. The primary outcome is Number of Participants Reporting a First Breakthrough HE Episode.

2. Clinical Question

The registry describes the trial purpose as evaluating whether rifaximin alone or rifaximin with lactulose delays onset of hepatic encephalopathy in participants with cirrhosis and a previous episode. The primary outcome, however, is posted as a count of participants reporting a first breakthrough episode during the stated follow-up period. It is useful to distinguish that count-based outcome from the separate time-to-event analysis reported by the sponsor: the count records whether a participant had the event within the period, while a time-to-event analysis also uses information about when the event occurred.

The comparison is between assigned treatment strategies, not a comparison of lactulose alone against rifaximin alone. The registry identifies the study as randomized, open-label, active-controlled, and parallel-group. Treatment assignment was therefore randomized, but participants and investigators were not masked according to the record. The endpoint definition uses a change in Conn score to Grade 2 or higher as the threshold for a breakthrough episode. The record does not report whether the primary question was framed around a specified clinically important difference.

3. Trial Design

The registry identifies NCT01842581 as a completed Phase 4, randomized, open-label, active-controlled, parallel-group study sponsored by Bausch Health Americas, Inc. The recorded enrollment is 222. The study began on 2013-01-08, and the primary completion date is 2014-12-17. The registry lists hepatic encephalopathy and cirrhosis as conditions.

Participants were assigned to rifaximin 550 mg twice daily alone or rifaximin 550 mg twice daily with lactulose. Both assigned regimens were described for 24 weeks. In the combination group, lactulose was self-titrated to produce 2 to 3 soft stools per day. The study is open-label, so masking was not used. The registry does not report further details about allocation concealment or the procedures used to maintain treatment assignment.

The primary endpoint count is posted for 113 participants in the rifaximin-only group and 108 in the combination group. The primary population is described as the ITT population, defined in the record as all randomized participants who received at least one dose of study drug. That definition is narrower than a definition including every randomized participant regardless of treatment receipt. The record does not provide additional detail about exclusions from the analysis or the handling of participants without complete follow-up.

The primary outcome timeframe runs from randomization (Day 1) up to Day 170. The secondary hospitalization outcome uses the same stated timeframe, while the all-cause mortality outcome runs from randomization through the end of study, Day 186. The registry lists six outcome measures and two posted secondary outcomes. It does not report the original trial sample-size justification, the detailed protocol, or whether interim analyses were planned or conducted.

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 222 participants with cirrhosis and in remission from demonstrated hepatic encephalopathy (HE) were enrolled and randomized in a 1:1 ratio to either Rifaximin 550 mg BID or Rifaximin 550 mg BID + Lactulose treatment arm.

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 received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants Reporting a First Breakthrough HE Episode, measured over From randomization (Day 1) up to Day 170.

The primary endpoint is the number of participants reporting a first breakthrough hepatic encephalopathy episode from randomization (Day 1) up to Day 170. The record defines a breakthrough episode as an increase in Conn score to Grade 2 or higher, including a change from Grade 0 or Grade 1 to Grade 2 or higher. Conn scoring describes mental state, ranging from no personality or behavioral abnormality at Grade 0 to coma at Grade 4.

The endpoint also has a time-to-event definition: the duration between the first dose of study drug and the first breakthrough episode. These are related but distinct summaries. A count of participants with an event within the follow-up period treats an event as present or absent for that interval. A time-to-event analysis incorporates the timing of the first event, and may also account for participants whose event status is not observed for the full period, depending on the analysis approach. The registry does not provide all details of that handling.

Using a threshold based on a change in mental-state score provides an operational way to identify a breakthrough episode. The threshold and the stated follow-up period define what the primary count represents; it is not a count of every possible change in symptoms or every later episode. The record does not report additional information about endpoint adjudication or assessment procedures.

7. Results Posted in the Registry

• Rifaximin 550 mg BID + Lactulose: 13.9% (15/108) versus 24.8% (28/113) on control; risk difference -10.9 percentage points (95% CI -21.2 to -0.6), risk ratio 0.56 (0.32–0.99); unadjusted two-proportion z-test p = 0.041.

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 Were Hospitalized Due to HE Episode

• 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 550 mg BID + Lactulose: 13.0% (14/108) versus 20.4% (23/113) on control; risk difference -7.4 percentage points (95% CI -17.2 to 2.4), risk ratio 0.64 (0.35–1.17); unadjusted two-proportion z-test p = 0.141.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rifaximin 550 mg BID + Lactulose and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants Who Died Due to Any Reason

• 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 550 mg BID + Lactulose: 1.9% (2/108) versus 1.8% (2/113) on control; risk difference 0.1 percentage points (95% CI -3.4 to 3.6), risk ratio 1.05 (0.15–7.30); unadjusted two-proportion z-test p = 0.964.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rifaximin 550 mg BID + Lactulose and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide a mixed level of information rather than an independent confirmation of the primary result. The hospitalization estimate points in the same direction as the primary count comparison, but its uncertainty interval includes no difference. The mortality comparison is highly imprecise, with few posted events and an interval that permits differences in either direction. Together, these outcomes do not establish a consistent, precise pattern across all outcomes.

Secondary outcomes can add useful context because they address consequences beyond the primary endpoint. Hospitalization due to an encephalopathy episode is related to the clinical event being studied, while all-cause mortality is a broader outcome. Neither is a substitute for the primary endpoint, and the distinct follow-up windows should be kept in mind when interpreting them.

The registry does not report a multiplicity adjustment or a hierarchy for interpreting secondary tests. General explanation: when several outcomes are tested, the chance of at least one apparently unusual result can increase, even if there are no true effects. Unadjusted secondary p-values therefore carry less confirmatory weight than a single prespecified primary test, particularly when the analysis plan and testing order are not reported. The secondary results are appropriately read as descriptive and exploratory evidence, not as definitive proof of benefit, harm, or equivalence on those outcomes.

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

• Number of Participants Who Were Hospitalized Due to HE Episode
• Number of Participants Who Died Due to Any Reason

9. Statistical Interpretation

10. Statistical Methods Explained

What does the count-based recalculation compare?

The recalculation uses the posted number of participants with the event and the posted group sizes to estimate an unadjusted difference in event risk. Risk is the proportion of participants in a group who experienced the defined event during the stated period. The risk difference subtracts one group’s risk from the other’s. A value below zero for combination minus rifaximin alone corresponds to a lower observed event proportion in the combination group. This is a simple comparison of the posted summary data; it does not adjust for other participant characteristics or reconstruct individual follow-up histories.

The estimate is accompanied by a confidence interval and a p-value. General explanation: a confidence interval describes a range of values reasonably compatible with the data under the method’s assumptions. It conveys uncertainty about the estimated contrast; it is not a range containing a known true value with certainty. A p-value measures how unusual data at least this discordant with a specified null hypothesis would be if that null and the analysis assumptions held. It is not the probability that the null hypothesis is true, nor does it measure clinical importance.

How does the time-to-event analysis differ?

The sponsor’s primary analysis is reported using a hazard ratio and score statistics. General explanation: a hazard is an event rate at a particular time among participants who have not yet had the event. A hazard ratio compares those rates over follow-up under the analysis model. It is not the same quantity as a difference in the proportions with an event by a fixed time. A time-to-event method can use event timing rather than reducing every participant to an event/no-event status at the end of follow-up. The registry does not report the full model specification, censoring details, or the reference direction for the reported ratio.

The sponsor labels its analysis non-inferiority. General explanation: a non-inferiority analysis asks whether the data exclude an unacceptable loss relative to a prespecified margin. The margin and the full decision criteria are necessary to interpret such a result. Neither is reported in the registry record, so the label alone is not enough to establish that the non-inferiority criterion was met.

Why can the two methods yield different-looking results?

General explanation: analyses can differ because they target different estimands, use different information, and rely on different assumptions. A count-based risk difference summarizes event status over a defined interval. A hazard ratio summarizes relative event rates over time under its model. Differences in endpoint timing, censoring, event coding, or model specification can affect those estimates. The registry’s posted count data do not permit a full independent reconstruction of the sponsor’s time-to-event calculation.

Why does over-dispersion matter?

General explanation: over-dispersion occurs when variability in data exceeds what a statistical model assumes. It can lead to uncertainty estimates that are too narrow if ignored. It is especially relevant for some count outcomes and clustered data. The primary outcome is posted as participants with an event, rather than as a repeated-event count, and the registry does not report an over-dispersion assessment. No conclusion about that issue can be drawn from the posted summaries alone.

What does randomization contribute?

General explanation: random assignment aims to make treatment groups comparable on average with respect to measured and unmeasured baseline factors. It supports a causal interpretation when allocation, follow-up, outcome measurement, and analysis are appropriately handled. It does not ensure that every realized sample is balanced, and it does not remove concerns about missing outcomes or post-randomization exclusions. The registry identifies the trial as randomized, but detailed allocation procedures and sensitivity analyses are not reported.

The unadjusted recalculation and the sponsor’s reported analysis should therefore be read as complementary descriptions, not interchangeable estimates. The posted summaries support a straightforward comparison of event counts, while fuller assessment of the sponsor’s time-to-event result would require analysis details that are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference confidence interval runs from -0.212 to -0.006. Because the interval does not include zero, it is consistent with an unadjusted difference in event risk favoring the combination group under the stated comparison direction. The upper endpoint is close to zero, while the interval also allows a larger difference. This span illustrates why the point estimate should not be read as an exact description of the treatment contrast.

General explanation: a confidence interval reflects both the observed data and the statistical method used to analyze them. A narrower interval indicates greater precision for the particular estimand and assumptions; a wider interval indicates more uncertainty. It does not account for biases that may arise from missing data, unmasking, outcome measurement, or a model that does not fit the data. A confidence interval that excludes zero is not proof of an important effect, and one that includes zero does not prove that there is no effect.

The sponsor’s time-to-event estimate has a 95% confidence interval from 1.045 to 3.672. This is a broad range on the hazard-ratio scale. Its interpretation depends on the event and reference-group coding, which are not explained in the record. It should not be treated as interchangeable with the risk-difference interval.

Precision is more limited for the secondary outcomes. The hospitalization interval includes zero, and the mortality interval is also compatible with differences in either direction. Sparse mortality events make the estimate particularly uncertain. These intervals describe what the posted data can support; they do not establish equivalence between groups.

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 primary planning figures are participants per arm, because the primary outcome is a binary participant-level event count and the stated planning assumptions specify per-arm figures for outcomes other than time-to-event analyses. The time-to-event convention in the registry’s planning description is total events, but that convention does not apply to the primary count-based planning figures. The trial’s original design assumptions and sample-size justification are not reported in the registry record.

The planning illustration uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It considers detecting the stated fraction of the observed effect. The row for 100% uses the observed effect as the planning target; the rows for 75% and 50% use smaller effects. The figures are 206 participants per arm for 80% power and 275 participants per arm for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the corresponding figures are 386 and 515 participants per arm. For 50% of the observed effect, they are 910 and 1,217 participants per arm.

In plain language, 80% power is the planned chance of detecting the specified effect under the calculation’s assumptions if that effect is truly present. The 90% power column uses a higher target chance of detection, which requires more participants under the same assumptions. Smaller target effects require more participants because they are harder to distinguish from random variation. These are planning illustrations based on the observed effect, not observed power and not evidence about the trial’s original design.

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 = 0.248; treatment proportion p₁ = 0.139; average p̄ = 0.193.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5585 = 1.0946.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5532 = 0.4656.
4. n = (1.0946 + 0.4656)² / (-0.1089)² = 205.3, rounded up to 206 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 <- 0.247787610619469                          # control proportion
p1 <- 0.138888888888889                          # 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(1842581)
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 = 206 (80% power), 275 (90% power)
 75% of observed effect: n per arm = 386 (80% power), 515 (90% power)
 50% of observed effect: n per arm = 910 (80% power), 1,217 (90% power)
power.prop.test: 205.3 
Simulated power at n = 206 per arm: 0.803 (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 sponsor’s primary analysis is posted as a non-inferiority time-to-event analysis using score statistics. It reports a hazard ratio of 1.959, a 95% confidence interval from 1.045 to 3.672, and p = 0.036. The registry does not report the non-inferiority margin, full analysis specification, or hazard-ratio reference direction. Those omissions limit interpretation of what the reported result establishes about the non-inferiority question.

The unadjusted recalculation uses the primary participant counts and estimates a risk difference, rather than a hazard ratio. Its confidence interval runs from -0.212 to -0.006, and its p-value is 0.041. The two results are not direct replications of one another: one is based on event proportions by the stated endpoint period, while the other is a time-to-event analysis. Their estimates and p-values should not be compared as if they used the same scale or assumptions.

The record does not flag a discrepancy between the posted summary statistics and the recalculation. The recalculation is therefore best read as a transparent, unadjusted check of the count data, not a replacement for the sponsor’s reported analysis. The sponsor analysis remains the analysis reported for the trial’s stated non-inferiority framework, while its interpretation is constrained by the missing margin and methodological details.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists six outcome measures and posts two secondary outcomes in addition to the primary outcome. It does not report whether statistical testing across outcomes was adjusted for multiplicity, whether outcomes were ordered in a formal testing hierarchy, or whether any secondary analyses were designated as confirmatory. Without that information, the role of the secondary p-values in a formal decision process is not clear.

General explanation: testing several outcomes creates multiple opportunities to observe a nominally small p-value by chance. Methods such as a prespecified hierarchy or a multiplicity adjustment can control the overall error rate, but their interpretation depends on the plan set before results are examined. The registry record does not report whether such methods were used, so no claim about control of multiplicity is warranted.

The primary population is defined as randomized participants who received at least one dose of study drug. The record does not provide a full account of participants excluded from the analysis, the numbers with missing endpoint assessments, or the methods used to handle missing data. It also does not report sensitivity analyses for missing outcomes or departures from assigned treatment. These details matter because missingness and post-randomization exclusions can affect comparisons even in a randomized trial.

Masking was not used, according to the registry. General explanation: in an open-label study, knowledge of assigned treatment can potentially influence care, reporting, or assessment. The magnitude of any such influence cannot be determined from the posted summaries. Endpoint assessment procedures, independent adjudication, and safeguards against bias are not reported in the registry record.

Finally, although the sponsor labels the primary time-to-event analysis as non-inferiority, the margin and detailed statistical plan are not reported. The original sample-size assumptions, interim-analysis plans, and complete analysis populations are also not reported in the registry record. These gaps limit independent assessment of the confirmatory framework and the robustness of the posted results.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hepatic encephalopathy (18.6%), ascites (6.5%), renal failure acute (5.3%), anaemia (4.4%), urinary tract infection (3.7%).

The registry records serious adverse events among 43 of 113 participants in the rifaximin-only group and 35 of 108 in the combination group. The corresponding counts for participants with other, non-serious adverse events are 68 of 113 and 53 of 108. These are group-specific participant counts; they do not describe the severity, timing, duration, or causal relationship of each event.

The listed serious adverse event terms include hepatic encephalopathy at 18.6%, ascites at 6.5%, acute renal failure at 5.3%, anaemia at 4.4%, urinary tract infection at 3.7%, and cellulitis at 2.7%. The record does not assign these term percentages to treatment groups in the posted list, so they should not be interpreted as group-specific rates.

Serious adverse events and the primary efficacy endpoint are not interchangeable measures. The registry’s adverse-event counts do not by themselves establish that a treatment caused an event or that one regimen is safer. The adverse-event record lists deaths as unavailable, while the separate secondary outcome reports deaths due to any reason. Further details about event definitions, attribution, and comparative safety analyses are not reported in the registry record.

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

The posted primary counts show fewer participants with a first breakthrough episode in the rifaximin-plus-lactulose group than in the rifaximin-only group during the stated period. The unadjusted recalculation produces a risk-difference interval that does not include zero, while the sponsor reports a statistically significant time-to-event analysis labelled non-inferiority. These findings describe the posted analyses; they do not by themselves settle the clinical meaning of the contrast.

The result does not establish how large a difference would matter to participants, because the registry does not report a threshold for clinical importance. It also does not show that every participant in one group had a better outcome than a participant in the other group. Group-level event counts and model estimates describe average patterns, not individual outcomes.

The result does not establish a definitive effect on hospitalization or mortality. The hospitalization comparison is uncertain, and the mortality estimate is particularly imprecise. Nor does the primary result establish a complete safety comparison: adverse-event summaries need to be interpreted with their definitions, follow-up, event attribution, and missing information in mind.

The study was open-label, and the registry does not provide full details on outcome assessment, missing-data handling, or the time-to-event model. The sponsor’s non-inferiority margin is also not reported. Those limitations constrain the conclusions that can be drawn from the record. The findings are specific to the studied population, assigned regimens, and follow-up periods; generalization beyond those circumstances is not established by the posted data.

18. Why This Trial Matters Statistically

This trial is statistically instructive because it reports both participant counts and a time-to-event analysis for the primary outcome. Those approaches answer related but nonidentical questions. A risk difference communicates the contrast in event proportions over a fixed period, while a hazard ratio summarizes event rates over time under a model. Treating the two estimates as interchangeable would obscure the different information and assumptions behind them.

The primary count-based recalculation is relatively easy to understand, but its confidence interval also shows why the point estimate alone is insufficient. The reported interval lies on one side of zero while approaching it at one end, indicating uncertainty about the size of the contrast. Statistical evidence against a no-difference null does not automatically indicate a large or important effect.

The non-inferiority label makes the missing design details especially consequential. A non-inferiority conclusion depends on a prespecified margin and analysis choices; the registry record does not report the margin or full plan. This illustrates why a p-value and hazard ratio cannot, on their own, convey the full logic of a non-inferiority claim.

The secondary results also demonstrate the importance of precision and multiplicity. They address relevant outcomes, but their uncertainty and the lack of a reported testing hierarchy limit their confirmatory role. Reading the primary and secondary evidence together requires attention to estimands, confidence intervals, endpoint timing, analysis populations, and reporting gaps—not just whether individual p-values cross a conventional threshold.

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 registry record leaves several trial-specific uncertainties. The sponsor reports a non-inferiority analysis, but the non-inferiority margin is not reported. The hazard-ratio reference direction and complete model specification are also not reported, making the sponsor’s numerical result difficult to interpret independently beyond its recorded label and statistics.

The primary analysis population is defined as randomized participants who received at least one dose. The record does not report the number of randomized participants who did not receive treatment, the reasons for any exclusions, or whether additional analysis populations were used. Missing-outcome counts, imputation or censoring procedures, and sensitivity analyses are not reported. These omissions make it harder to judge robustness to incomplete follow-up.

The trial was open-label. The registry does not report whether outcome assessors were masked, whether breakthrough events were independently adjudicated, or how treatment knowledge was prevented from influencing assessment. Such details are relevant to an outcome involving clinical scoring and episode classification.

The registry also does not report the original sample-size rationale, interim-analysis plan, or a complete multiplicity strategy. The posted planning illustration is based on the observed effect and is not a substitute for the trial’s original design justification. The adverse-event list does not provide all group-specific term-level detail, and the record does not report event attribution methods. These limitations do not negate the posted results, but they restrict how completely they can be assessed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: The Safety/Efficacy of Rifaximin With/Without Lactulose in Participants With A History of Recurrent Hepatic Encephalopathy — NCT01842581.
• Registry record last updated 2019-09-09; status last verified 2019-09.
• Results first posted 2019-09-09.
• 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

NCT01842581 is a completed, randomized, open-label, parallel-group Phase 4 trial comparing rifaximin 550 mg twice daily with the same rifaximin regimen plus lactulose in participants with a history of recurrent hepatic encephalopathy and cirrhosis. Recorded enrollment is 222, and both assigned regimens were described for 24 weeks.

The primary outcome was the number of participants reporting a first breakthrough hepatic encephalopathy episode through Day 170. The posted counts were 28 of 113 with rifaximin alone and 15 of 108 with rifaximin plus lactulose. The unadjusted recalculation favors the combination group, while the sponsor reports a time-to-event non-inferiority analysis. The registry does not report the non-inferiority margin or enough methodological detail to fully evaluate that analysis.

Secondary outcomes covered hospitalization due to hepatic encephalopathy and death from any cause. Their estimates are less conclusive, and multiplicity handling is not reported. Missing-data procedures, the original sample-size justification, and several analysis details are also not reported in the registry record.