Rifaximin Therapy in Chronic Kidney Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Rifaximin Therapy in Chronic Kidney Disease (NCT02342639), a randomized phase 4 study. The primary outcome is Change in Serum Trimethylamine N-oxide (TMAO).

2. Clinical Question

3. Trial Design

The registry identifies NCT02342639 as a completed Phase 4 randomized trial of rifaximin therapy in chronic kidney disease. Its official title is “Impact of Rifaximin Therapy on Intestinal Byproducts in Chronic Kidney Disease.” The listed sponsor is Jason Stubbs, MD. The registry records a start date of 2015-06 and a primary completion date of 2019-03-01.

The design is described as randomized, triple-masked, and parallel. In a parallel-group design, participants are assigned to a study group and receive that group’s intervention rather than crossing over between interventions. Random allocation is intended, in general, to reduce systematic differences between groups at baseline. Masking can reduce the influence of knowledge about assignment on care, measurement, or assessment. The registry does not say which participants, clinicians, outcome assessors, or other roles were masked, nor does it report details of the allocation procedure.

The intervention was a 10-day course of rifaximin, compared with a 10-day course of placebo. The primary endpoint was change in serum TMAO from baseline to Day 11. C-reactive protein and change in serum interleukin-6 (IL-6) were listed as secondary outcomes, also assessed as change from baseline to Day 11. The registry’s timeframe for IL-6 uses “day 11”; it does not report additional assessment schedules.

The registry lists enrollment as 38. Outcome-specific arm sizes are reported with the results, and those figures need not be interpreted as the enrollment count: outcome availability and the registry’s enrollment field describe different aspects of the record. Reasons for any difference between enrollment and outcome arm counts are not reported in the registry record. Eligibility criteria, baseline participant characteristics, details of treatment adherence, and the original sample-size justification 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.

Overall Study

Reasons for not completing this period:

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.

6. Primary Endpoint

The registry lists the primary outcome as Change in Serum Trimethylamine N-oxide (TMAO), measured over Change from baseline to Day 11.

The primary endpoint is the mean change in serum trimethylamine N-oxide (TMAO), measured in uM, from baseline to Day 11. TMAO is identified in the registry as a bacterial byproduct of interest. The endpoint therefore captures the change over the stated interval in a measured serum concentration, rather than a clinical event or a longer-term outcome. The registry’s stated study purpose also included serum and urine bacterial byproducts, inflammatory markers, and stool bacterial content, but the primary outcome is specifically serum TMAO.

A change score compares a participant’s measurement at follow-up with that participant’s baseline measurement. Using change as an endpoint focuses the comparison on how the measured quantity moved over the specified interval. The posted group means are -3.9 uM for rifaximin and 0.5 uM for placebo. The posted comparison expresses the mean difference as rifaximin minus placebo and estimates it as -4.4 uM. The registry reports standard deviations to describe spread among participant-level changes within each arm.

This biomarker endpoint can address whether the measured concentration changed differently between the groups during the stated period. It does not, by itself, establish what a change means for symptoms, kidney function, future health, or other clinical outcomes. Those outcomes are not reported as the primary endpoint in the registry record. Nor does the endpoint reveal whether changes in serum TMAO corresponded to changes in urine measures or stool bacterial content; those relationships are not reported in the registry record.

7. Results Posted in the Registry

• Rifaximin: mean -3.90 versus 0.50 on control; difference -4.40 (95% CI -13.25 to 4.45), standardized effect d = -0.34; z-test p = 0.330.

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.

C-reactive Protein

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Rifaximin: mean 6.00 versus -2.60 on control; difference 8.60 (95% CI -1.25 to 18.45), standardized effect d = 0.57; z-test p = 0.087.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rifaximin and the control. The interval gives the range of effects that remain compatible with the data.

Change in Serum Interleukin-6 (IL-6)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Rifaximin: mean 0.30 versus 0.80 on control; difference -0.50 (95% CI -1.72 to 0.72), standardized effect d = -0.31; z-test p = 0.421.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rifaximin and the control. The interval gives the range of effects that remain compatible with the data.

Across the two secondary biomarkers, the estimates point in different directions under the reported subtraction order: the C-reactive protein mean difference is positive, while the IL-6 mean difference is negative. Both confidence intervals include zero, and neither unadjusted p-value alone provides a clear resolution of the corresponding group difference. Taken together, these outcomes do not form a consistent pattern of precise separation across the reported inflammatory markers.

The secondary outcomes relate to the primary result by broadening the biomarker picture beyond serum TMAO. The primary result also has a confidence interval that includes zero, so the posted results do not show a clearly resolved difference across the primary and secondary biomarkers. The registry’s stated purpose also refers to serum and urine bacterial byproducts and stool bacterial content, but the posted secondary results are C-reactive protein and IL-6. Further results for urine measures or stool bacterial content are not reported in the registry record.

Secondary findings generally carry less weight when many outcomes are examined without a reported plan for controlling multiplicity. Each additional comparison creates more opportunity for an apparently unusual result to arise by chance, even when there is no real difference. The registry does not report a multiplicity adjustment, a hierarchy of outcomes, or the prespecified status of the secondary analyses. Their unadjusted p-values therefore should not be treated as confirmatory evidence on their own. The record also lists no reported analyses for the secondary endpoints, limiting information about whether any additional planned analyses were conducted.

The summaries do not establish whether the biomarkers are related to one another at the participant level, whether their changes track with clinical outcomes, or whether one endpoint was intended to support another. Such relationships and the rationale for endpoint prioritization are not reported in the registry record. The secondary results are best read as estimates with uncertainty that add context, rather than as independent proof of a broader treatment effect.

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

• C-reactive Protein
• Change in Serum Interleukin-6 (IL-6)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean change represent?

General statistical explanation: For a continuous measure, a mean is an average across the observations included in the analysis. A mean change summarizes the average movement from baseline to follow-up. It does not show how every participant changed: some values may rise, some may fall, and some may remain close to baseline. The registry identifies the reported measure as a mean and gives standard deviations for the arm-level changes. The standard deviation describes variability among participant changes; it is not the same as the uncertainty in the estimated group mean or group difference.

For TMAO, the arm-level means are -3.9 uM for rifaximin and 0.5 uM for placebo. The comparison is reported as a mean difference, with the comparison direction defined by rifaximin relative to placebo. The estimate is -4.4 uM. A negative estimate means the average change was lower in the rifaximin group than in the placebo group under that subtraction order. It does not mean that every person’s TMAO declined, and it does not by itself establish that the intervention caused a change.

What does the confidence interval add?

General statistical explanation: A confidence interval describes a range of values for the underlying effect that are compatible with the data and the statistical model at the stated confidence level. It communicates uncertainty around an estimate, rather than giving a range in which a specified proportion of individual participant values lie. The primary comparison’s reported 95% confidence interval is -13.25 to 4.452 uM. Since this interval contains zero, the data do not distinguish a zero mean difference from differences in either direction at that interval level. The interval also shows that the estimate is uncertain: effects appreciably below or above the point estimate remain compatible with the reported results.

A confidence interval depends on the analysis assumptions and the data available for that analysis. The registry does not report enough detail to independently assess all model choices, missing observations, or any adjustments beyond the posted summary. The interval should therefore be interpreted as the uncertainty measure reported with the comparison, not as a guarantee about the true effect.

How should the p-value be read?

General statistical explanation: A p-value measures the compatibility of the data with a null hypothesis under a statistical model. It is not a measure of the probability that the treatment has no effect, nor does it quantify the probability that findings will replicate. It also does not measure clinical importance. The primary unadjusted p-value is 0.33. That value, considered alongside the estimate and confidence interval, indicates that the observed data do not provide a sharply resolved estimate of the between-group difference. The registry does not report the trial’s prespecified statistical analysis plan or a prespecified threshold for interpreting p-values, so claims about planned hypothesis-testing decisions are not justified from the record.

Why do standard deviations matter?

General statistical explanation: A standard deviation describes how dispersed individual observations are around a group mean. Greater dispersion can make a mean difference harder to estimate precisely when sample sizes are limited. The posted standard deviations for primary-outcome change are 15.4 uM in the rifaximin group and 9.5 uM in the placebo group. These values describe variation in participant changes, not the confidence interval for the difference. The posted confidence interval incorporates uncertainty in the comparison, which depends on group sizes and variability under the analysis used.

For a continuous outcome, the mean is a useful summary when the mean itself answers the scientific question and the data can be reasonably described by that summary. The registry does not report outcome distributions, so the extent of skewness, outliers, or other distributional features cannot be assessed from the record. A general concern with unusually skewed data is that the mean and standard deviation can be sensitive to extreme values. Whether that concern applies to these trial data is not reported in the registry record.

What can randomization and masking contribute?

General statistical explanation: Random allocation helps make treatment groups comparable on average, including on factors that may not be measured, but it does not guarantee exact balance in a particular trial. Masking can reduce the opportunity for expectations to influence participant behavior, clinical management, or outcome assessment. The registry identifies the trial as randomized and triple-masked. It does not describe the randomization method, concealment process, identities of the masked roles, or whether masking was assessed. Consequently, those design labels can be reported, but the implementation cannot be evaluated from this record.

The parallel-group structure means the reported group comparison is between the rifaximin and placebo arms. The posted analysis is a difference in mean changes, rather than a within-person comparison of rifaximin against placebo. The group-level estimate does not show individual treatment responses.

What limits the analysis description?

The registry lists zero analyses and does not include reported secondary-outcome analyses. It gives arm-level sample sizes and summary statistics, but does not report an analysis population, covariate adjustment, missing-data method, sensitivity analysis, or multiplicity procedure. These details matter because choices about which observations are included and how missing measurements are handled can affect an estimate. The original statistical plan, including whether the analysis was prespecified and how the primary result was intended to be tested, is not reported in the registry record.

The results are continuous-outcome summaries at a specified assessment time. They do not describe time-to-event outcomes, and no event-time method is reported. The posted values permit interpretation of the stated means, standard deviations, mean differences, confidence intervals, and unadjusted p-values, but not a reconstruction of an unreported model or a verification using participant-level data.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a quantity, not whether that quantity is clinically important. The primary mean difference is -4.4 uM, with a 95% confidence interval from -13.25 to 4.452 uM. The estimate points toward a lower mean change in the rifaximin group under the stated subtraction order, but the interval spans zero and also includes values on either side. Thus, the direction and size of the underlying difference remain uncertain. The interval is the key measure of that uncertainty; the point estimate alone would give an incomplete picture.

The reported primary arm standard deviations are 15.4 uM for rifaximin and 9.5 uM for placebo, with outcome sample sizes of 17 and 14. These arm-level summaries show that participant changes varied within each group. They do not identify the distribution of changes, the presence of influential observations, or the extent of missing measurements. Those details are not reported in the registry record.

The two secondary comparisons also have confidence intervals that include zero: -1.245 to 18.45 ug/ml for C-reactive protein, and -1.718 to 0.718 pg/ml for IL-6. Their widths indicate that the estimates do not sharply resolve the underlying differences. Confidence intervals should be considered together with the outcome scale and the study’s scientific question; no threshold for a clinically important difference is reported in the registry record.

These intervals reflect the uncertainty represented by the posted comparisons, under their analysis assumptions. They do not account for every possible source of uncertainty, such as selective outcome reporting or unreported analytic choices. The registry does not report the original statistical plan, missing-data methods, or sensitivity analyses. Accordingly, the posted precision is informative but does not eliminate uncertainty about how robust the estimates are to those choices.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total event counts. They are illustrations based on the observed effect rather than a report of the original trial’s design justification. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario uses the stated fraction of the observed effect as the effect to detect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a planning scenario designed to have an 80% chance of detecting the specified effect if that effect is present, under the stated assumptions. The 90% power column gives the corresponding per-arm planning number for a higher chance of detection under those assumptions. For the primary endpoint, planning for 100% of the observed effect gives 139 participants per arm for 80% power and 186 for 90% power. Planning for 75% of the observed effect gives 247 participants per arm for 80% power and 331 for 90% power; planning for 50% gives 556 and 744, respectively.

The same pattern applies to the secondary outcomes: the estimates increase when the target effect is a smaller fraction of the observed effect, and the 90% power target requires more participants per arm than the 80% target at the same effect assumption. Smaller effects are harder to distinguish from random variation, so they require more participants for the same planned power, all else held constant. The figures are planning illustrations, not observed power. They do not describe the probability that this completed trial reached a statistically significant result, and they should not be treated as the original design plan.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -4.400; pooled standard deviation σ = 13.088.
2. n = 2 × (1.96 + 0.842)² × 13.088² / -4.400² = 138.9, rounded up to 139 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
delta <- -4.4                      # observed difference in means
sigma <- 13.0883074957554                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2342639)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 139 (80% power), 186 (90% power)
 75% of observed effect: n per arm = 247 (80% power), 331 (90% power)
 50% of observed effect: n per arm = 556 (80% power), 744 (90% power)
power.t.test: 139.9 
Simulated power at n = 139 per arm: 0.799 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 lists one primary outcome and two secondary outcomes in the posted results. It does not report how the statistical plan addressed the possibility of multiple comparisons. When several outcomes are tested, the chance of at least one result appearing statistically notable by chance can increase. A prespecified hierarchy, adjustment procedure, or other multiplicity strategy can help define how results should be interpreted, but none is reported in the registry record. The secondary p-values are described as unadjusted and should be read with that limitation in mind. The registry does not say whether any outcomes were added, removed, or changed after study initiation.

Missing-data handling is also not reported in the registry record. The primary-outcome arm sizes are 17 for rifaximin and 14 for placebo, while the registry enrollment field lists 38. The record does not explain why these figures differ or whether the outcome sample sizes reflect missing measurements, exclusions, or another reason. It does not report the number or pattern of missing observations, the approach to incomplete baseline or follow-up measurements, or any sensitivity analysis addressing missingness.

The analysis population is not reported in the registry record. The record does not specify whether results were based on all randomized participants, participants who completed treatment, participants with available measurements, or another defined population. It also does not report protocol deviations, adherence information, or rules for excluding observations. Without these details, the estimates can be interpreted as the posted summaries but cannot be assigned confidently to a particular analysis population.

The registry lists no reported analyses overall and no reported analyses for the secondary outcomes. It does not provide a statistical analysis plan, adjustment variables, model diagnostics, or confirmatory sensitivity analyses. These omissions do not change the numerical results that are posted, but they limit assessment of how the analyses were selected and how robust they may be to alternative assumptions. The original design assumptions and the trial’s planned approach to multiplicity and missing data are not reported in the registry record.

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 non-serious adverse event terms

The registry reports serious adverse events for participants considered at risk in each arm. In the rifaximin group, 17 were at risk and 0 serious adverse events were reported; in the placebo group, 14 were at risk and 0 serious adverse events were reported. Deaths are reported as 0 in each group. These are counts from the registry record and should not be read as proof that no serious events could occur outside the recorded observation or reporting process.

The record also reports 1 other, non-serious adverse event in the rifaximin group and 2 in the placebo group, with 17 and 14 participants at risk respectively. The registry does not list serious-event terms, and it does not provide event descriptions for the other adverse events in the posted safety data. The observation period for safety, definitions used for each category, event timing, and relationship to treatment are not reported in the registry record.

These figures are descriptive counts, not a complete assessment of comparative safety. With limited details about event ascertainment, duration, and reporting, the counts cannot establish that the groups had equivalent risk or that an event was caused by a particular treatment. They should be interpreted only as the adverse-event figures recorded for this trial.

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

The posted primary result estimates a difference in mean change in serum TMAO between the rifaximin and placebo groups from baseline to Day 11. The estimate is -4.4 uM, and the 95% confidence interval extends from -13.25 to 4.452 uM. This indicates uncertainty about both the direction and size of the underlying difference. The unadjusted p-value is 0.33. The result does not provide a precise demonstration of a between-group difference, but it also does not establish that the true difference is exactly zero.

The endpoint is a short-interval biomarker measure. It does not directly report symptoms, kidney function, longer-term disease progression, or another clinical outcome. The registry’s study purpose mentions serum and urine bacterial byproducts, inflammatory markers, and stool bacterial content, but the posted outcome results do not establish whether changes in these measures translate into changes that matter to participants. The clinical importance of a given TMAO change is not reported in the registry record.

Randomization and masking are features of the registered design, but the available record does not describe how those procedures were implemented or the details of the analysis population. The registry also does not report missing-data handling, the full statistical plan, or multiplicity procedures. These gaps mean that the posted numerical results should not be expanded into claims about all randomized participants, unreported outcomes, or robustness under alternative analyses.

The secondary biomarker comparisons provide additional estimates, but their confidence intervals include zero and the analyses are reported as unadjusted. They do not establish a coherent, precise pattern across the biomarkers. The safety data report no serious adverse events and no deaths in either group, along with counts of other adverse events; limited safety-reporting details prevent those figures from settling broader safety questions.

In short, the registry record documents a randomized comparison and reports biomarker estimates with substantial uncertainty. It does not establish a clinical benefit, a lack of benefit, or a definitive safety conclusion. Interpretation should remain tied to the measured endpoints, the specified assessment time, and the limitations of the registry information.

17. Why This Trial Matters Statistically

This trial offers a useful example of why a point estimate should not be interpreted without its uncertainty. The primary comparison is reported as a mean difference of -4.4 uM, but the 95% confidence interval ranges from -13.25 to 4.452 uM. The point estimate alone suggests a direction; the interval makes clear that the data leave substantial uncertainty about the size and even the direction of the underlying difference. The p-value is another part of that inferential picture, not a replacement for the estimate and interval.

The record also illustrates the distinction between a registry enrollment figure and outcome-specific sample sizes. Enrollment is listed as 38, while the primary outcome reports arm sizes of 17 and 14. The record does not explain this difference. Transparent accounting of participant flow, missing measurements, and analysis populations helps readers understand which data contributed to an endpoint and how the results should be generalized.

Another statistical issue is the interpretation of multiple biomarkers. A primary outcome and secondary outcomes can address related but distinct questions. Without a reported plan for multiplicity or an outcome hierarchy, secondary unadjusted results should not be treated as confirmatory simply because their p-values may appear notable. Their estimates and confidence intervals remain valuable descriptive information, but they have a different evidential role.

Finally, planning illustrations based on an observed effect do not reconstruct a trial’s original design rationale. They show how assumed target effects and power goals relate to participant requirements under stated planning assumptions. The registry’s original sample-size justification is not reported. Keeping that distinction clear prevents retrospective planning calculations from being mistaken for the study’s actual design process or evidence of the probability that its result was detectable.

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 contains limited information for judging how representative the trial population was. It identifies chronic kidney disease as the condition but does not report eligibility criteria, disease stage, baseline characteristics, or other clinical features. The posted outcome sample sizes are smaller than the enrollment figure, and the reason is not reported in the registry record. Without participant flow and missing-data information, the scope of the analyzed population is uncertain.

The intervention period is described as a 10-day course, and the primary and secondary biomarker timeframes are changes from baseline to Day 11. Longer-term measurements and clinical outcomes are not reported in the registry record. The study purpose refers to urine measures and stool bacterial content, but results for those measures are not included among the posted outcomes. The interpretation therefore cannot extend to those unreported measurements.

The record does not report the statistical analysis plan, analysis population, handling of missing data, covariate adjustments, sensitivity analyses, or multiplicity methods. It also does not report distributional information that would allow assessment of whether means and standard deviations capture the outcome data well. No reported analysis records are listed. These omissions limit independent assessment of analysis choices and robustness.

For safety, the record gives counts but not event descriptions, timing, duration of observation, or attribution. The absence of reported serious adverse events and deaths should therefore be interpreted as a description of the registry data, not as a comprehensive estimate of safety. The record also does not report the trial’s original sample-size assumptions or justification. Together, these trial-specific gaps constrain how much can be inferred beyond the posted short-term biomarker summaries.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Rifaximin Therapy in Chronic Kidney Disease — NCT02342639.
• Registry record last updated 2021-11-05; status last verified 2021-10.
• Results first posted 2021-11-05.
• 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

NCT02342639 is recorded as a completed Phase 4 randomized, triple-masked, parallel-group trial in chronic kidney disease. Participants received a 10-day course of rifaximin or placebo. The primary outcome was mean change in serum TMAO from baseline to Day 11. The posted mean difference was -4.4 uM, with a 95% confidence interval from -13.25 to 4.452 uM and an unadjusted p-value of 0.33.

The registry also reports C-reactive protein and IL-6 as secondary outcomes. Their estimates are uncertain, and multiplicity handling is not reported in the registry record. Serious adverse events and deaths are recorded as 0 in each arm; other adverse-event counts are 1 and 2. The record does not report the original sample-size justification, analysis population, missing-data methods, or a full statistical analysis plan. Overall, the results describe short-term biomarker changes and their uncertainty, rather than clinical outcomes.