Rifaximin for the Treatment of Persistent Symptoms in Patients With Celiac Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Rifaximin for the Treatment of Persistent Symptoms in Patients With Celiac Disease (NCT01137955), a randomized na study. The primary outcome is Baseline Gastrointestinal Symptom Rating Scale (GSRS) Score.

2. Clinical Question

3. Trial Design

This was a randomized, triple-masked, parallel-group trial sponsored by Columbia University. The registry lists the study as completed, with enrollment of 50. The recorded study start was 2006-10, and primary completion was 2008-04. The phase is listed as NA. The registry does not report the method used to generate or conceal the random assignment, or which parties were masked.

The treatment groups were rifaximin and placebo. Rifaximin was described as 400 mg three times a day for 10 days; placebo pills were also given three times a day for 10 days. The posted baseline outcome summaries give n 20 for rifaximin and n 21 for placebo. The reason the outcome denominators differ from the enrollment figure is not reported in the registry record. These figures should be read as the denominators attached to the posted outcome summaries, not as an explanation of participant flow.

The primary outcome is named as the baseline GSRS score at week 0. The record also lists one secondary outcome: the percentage of participants with an abnormal breath test, assessed up to 12 weeks. The trial description says the study sought to assess symptom relief and breath-test results, but the listed primary outcome is at baseline. The registry does not provide a later GSRS result in the posted primary outcome, so the primary comparison cannot establish how symptoms changed after treatment.

Other design details, including the trial’s original sample-size assumptions, the planned analysis populations, and any interim analyses, are not reported in the registry record. The posted planning illustrations are based on the observed effects and are not evidence of the assumptions used when the trial was designed.

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: Fifty participants were enrolled and 41 participants completed the trial.

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 Baseline Gastrointestinal Symptom Rating Scale (GSRS) Score, measured over Baseline (week 0).

The primary outcome is the Gastrointestinal Symptom Rating Scale (GSRS) score at baseline, identified as week 0. The registry describes the GSRS as a validated seven-point questionnaire covering five symptom areas: abdominal pain, reflux, indigestion, diarrhea, and constipation. Individual symptom-area scores are combined by taking their mean to derive an overall score. The stated range is 0–7, with higher scores indicating greater gastrointestinal discomfort.

A standardized symptom measure can make symptom burden more systematic to describe than an unstructured report. It also allows a numerical summary of several gastrointestinal symptom areas. In this record, however, the primary endpoint is specifically a baseline score. Such a measurement can describe the groups’ starting symptom scores, but it does not show symptom improvement or worsening during follow-up. A treatment effect on symptoms would ordinarily require a post-baseline comparison, a change-from-baseline analysis, or another specified follow-up measure. No such primary GSRS result is posted in the registry record.

The registry gives group means and standard deviations for the baseline score. These summaries support a comparison of the recorded starting scores, but they do not show individual participants’ scores, the distribution of scores, or how symptoms evolved after the 10-day treatment course. The registry does not report a threshold for interpreting the size of a GSRS difference as important to patients.

7. Results Posted in the Registry

• Rifaximin: mean 2.70 versus 2.80 on control; difference -0.10 (95% CI -0.72 to 0.52), standardized effect d = -0.10; z-test p = 0.751.

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.

Percentage of Participants With Abnormal Breath Test

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Rifaximin: 10.0% (2/20) versus 19.0% (4/21) on control; risk difference -9.0 percentage points (95% CI -30.4 to 12.3), risk ratio 0.53 (0.11–2.56); unadjusted two-proportion z-test p = 0.413.
• 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.

The registry posts one secondary outcome: the percentage of participants with an abnormal breath test during follow-up of up to 12 weeks. There is therefore no broad pattern across several secondary endpoints to assess. This outcome addresses the study’s stated interest in whether rifaximin affected breath-test results, while the primary GSRS measure describes symptom scores at baseline.

The secondary comparison does not resolve the central limitation of the primary result. A breath-test classification is not a follow-up symptom score, and it cannot show whether symptoms improved. The outcomes measure different things and are recorded on different schedules. Their findings should not be combined into one general claim about symptom relief or treatment response.

The registry does not list reported analyses for the secondary outcome. The posted comparison is unadjusted, and the record does not say whether the secondary outcome was prespecified in a detailed analysis plan or whether any adjustment for multiple comparisons was intended. When several outcomes or comparisons are examined, unadjusted results carry less weight because the chance of an apparently notable result can rise across repeated testing. This is a general statistical concern, not evidence that any particular result in this trial is false.

The secondary result is best treated as limited information about the posted breath-test measure, with uncertainty reflected in its interval. It does not replace missing follow-up symptom results, and its interpretation depends on outcome completeness and analysis details that are not reported in the registry record. No additional secondary outcomes or reported analyses are available to establish whether the same pattern recurs across different measures.

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

• Percentage of Participants With Abnormal Breath Test

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods help distinguish what a result estimates from what it cannot establish. In this trial, the key distinction is between a baseline group comparison and a treatment effect measured after exposure to the assigned treatments. The registry identifies the primary GSRS outcome as a week-0 score. A week-0 comparison can characterize the groups at the start of the study. It cannot, on its own, estimate the effect of treatment on later symptoms.

What does a mean difference describe?

For a continuous outcome such as a symptom score, a mean is the arithmetic average of the recorded scores in a group. A mean difference compares those group averages. The posted comparison is expressed as the rifaximin mean minus the placebo mean. A negative value therefore indicates a lower recorded group mean for rifaximin, while a positive value indicates a higher one. Since higher GSRS scores indicate greater discomfort, direction can be described in relation to the scale. But the timing remains decisive: a difference in baseline means is not a difference in treatment response.

The standard deviations describe how spread out the individual scores are around their group means. The posted standard deviations are 1.1 for rifaximin and 0.9 for placebo. They are measures of variation among scores, not measures of uncertainty in the group means. The uncertainty in an estimated difference depends on both the observed variation and the amount of information contributing to the estimate. The registry does not post participant-level scores, so the distribution and any unusual observations cannot be examined from these summaries.

How should the confidence interval be read?

A confidence interval gives a range of estimates compatible with the data under the statistical procedure and its assumptions. For the posted mean difference, the interval extends from -0.717 to 0.517. Because it includes zero, the data are compatible with no difference in the group means as well as with differences in either direction. The interval’s breadth signals uncertainty about the size and direction of the baseline difference. It does not indicate a range of individual participants’ scores, and it is not a statement that a particular percentage of individual results fall within its bounds.

In general, a confidence interval is affected by the amount of data and the variability in the outcome. Greater variability or less information tends to produce less precise estimates. Precision is not the same as importance: even a precisely estimated difference could be too small to matter, while an imprecisely estimated result can leave a broad range of possibilities. The registry does not report a threshold for a clinically important GSRS difference, so clinical importance cannot be assessed from the numerical estimate alone.

What does the p-value add?

The unadjusted p-value for the primary comparison is 0.751. In general, a p-value measures the compatibility of the observed data, or more extreme data, with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not quantify the probability that a result occurred by chance. It also does not measure the size or clinical importance of an effect. Here, the p-value should be interpreted alongside the estimate, its confidence interval, and the fact that the measured outcome is at baseline.

The term unadjusted indicates that this p-value is not reported as adjusted for other outcomes or comparisons. The registry does not report whether a multiplicity adjustment was planned or performed. If researchers test several outcomes, the chance of obtaining at least one apparently notable result can increase; this is one reason unadjusted secondary results usually warrant more caution than a prespecified primary analysis. The registry’s reported-analysis listing is empty, so the complete analysis strategy cannot be checked against the posted results.

Why do outcome types matter?

The GSRS is continuous: it is recorded as a numerical score, and the primary summaries use means and standard deviations. The breath-test outcome is binary: each participant is classified according to whether the test was abnormal. A binary outcome can be summarized using group proportions and compared using measures such as a risk difference. In general, the risk difference subtracts one group’s event proportion from the other’s. Its confidence interval describes uncertainty in that absolute difference. Interpretation should account for how many observations contribute to the comparison, particularly when event counts are limited.

The registry lists the breath-test outcome as a percentage of participants with an abnormal test and gives a risk-difference comparison. It does not list reported secondary analyses. The outcome’s assessment window is up to 12 weeks, while the primary GSRS measure is at baseline. They therefore answer different questions: one describes the baseline symptom score, and the other concerns an abnormal breath-test classification during follow-up.

What can recalculated summaries establish?

Simple unadjusted calculations from posted summary statistics can describe a contrast and its uncertainty, but they cannot reproduce an analysis that depends on participant-level data, adjustment variables, or methods not documented in the registry. They also cannot resolve whether all randomized participants were included or how missing outcomes were handled. The registry record does not report those details. No discrepancy is flagged between the posted summaries and the recalculated comparisons, but the absence of a discrepancy does not supply the missing protocol or analysis plan.

Statistical interpretation therefore depends on matching each result to its endpoint, timing, and analysis population. For this trial, the baseline GSRS estimate is best read as a description of starting scores. It should not be recast as an estimate of post-treatment symptom relief. The breath-test result is a separate secondary outcome with its own uncertainty and limitations.

11. Confidence Intervals and Precision

The primary mean difference is -0.1, with a 95% confidence interval from -0.717 to 0.517. The interval includes zero and extends to values on either side of it. This means the observed summaries do not pin down a single direction for the baseline group difference. The point estimate alone is not a precise account of the range of differences compatible with the data.

Precision concerns the uncertainty in an estimate, not whether an effect is clinically meaningful. The registry does not report a threshold for a meaningful GSRS difference, so the interval cannot be divided into clinically important and unimportant values. The endpoint’s baseline timing also limits its interpretation: even a more precise baseline comparison would not measure symptom change after treatment.

For the breath-test comparison, the posted risk-difference interval is also broad and includes zero. It permits uncertainty in either direction, rather than a sharply determined difference between groups. The reported group sizes and event counts are limited, which makes it especially important to consider the interval rather than relying on the point estimate alone. No participant-level data are posted to examine the outcome distributions or individual patterns.

A confidence interval is not a guarantee about the true value, and it does not state where most individual outcomes lie. It quantifies uncertainty under the method used and its assumptions. Those assumptions, as well as the original analysis plan, are not fully reported in the registry record. The intervals therefore help show the uncertainty in the posted comparisons but cannot fill gaps in the study’s analysis documentation.

12. Planning a Similar Trial: Sample Size

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

The sample-size display is a planning illustration based on the observed effect, not a record of the trial’s original sample-size justification. For these continuous and binary outcomes, its figures are participants per arm, not total event counts. The 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 design assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm estimated to be needed, under those planning assumptions, for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning number for a 90% chance. These are conditional design calculations, not guarantees that a future study will detect an effect. The numbers are planning illustrations, not observed power for this completed trial.

The rows represent planning for 100%, 75%, and 50% of the observed effect. For the primary outcome, the figures for planning for 100% of the observed effect are 1,578 participants per arm for 80% power and 2,112 participants per arm for 90% power. For the secondary outcome, the corresponding figures are 237 and 317 participants per arm. The other rows show larger planning requirements for smaller fractions of the observed effects. In general, smaller effects require more participants to detect under otherwise unchanged assumptions.

The curve is a visual companion to the same planning exercise; it should be read as illustrating how planned sample size changes with the effect being targeted. These estimates depend on the observed effect, which can be unstable in a small study. They should not be treated as proof that the trial was originally designed around those targets, or as evidence about the trial’s actual statistical power.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.100; pooled standard deviation σ = 1.002.
2. n = 2 × (1.96 + 0.842)² × 1.002² / -0.100² = 1,577.4, rounded up to 1,578 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 <- -0.0999999999999996                      # observed difference in means
sigma <- 1.00243293784262                     # 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(1137955)
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 = 1,578 (80% power), 2,112 (90% power)
 75% of observed effect: n per arm = 2,805 (80% power), 3,755 (90% power)
 50% of observed effect: n per arm = 6,310 (80% power), 8,447 (90% power)
power.t.test: 1578.4 
Simulated power at n = 1,578 per arm: 0.793 (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

Multiplicity arises when several statistical comparisons are made. In general, repeated testing can increase the chance that at least one result appears notable even when no underlying effect exists. Researchers may address this through a prespecified hierarchy of outcomes, adjustment procedures, or careful interpretation of secondary analyses. The registry record does not report a multiplicity strategy, whether any adjustment was used, or how the primary and secondary outcomes were prioritized in the analysis plan. The one posted secondary outcome should consequently be read as secondary evidence rather than as an independent confirmation of the primary result.

The registry lists no reported analyses for the secondary outcome, and it does not provide a detailed analysis plan for the primary outcome. Interim analyses and any related decision rules are not reported in the registry record. These omissions mean the posted results cannot be checked against a documented plan for handling multiple outcomes or repeated looks at the data.

Missing-data methods and analysis populations are also not reported. The registry gives enrollment of 50 and outcome denominators of n 20 for rifaximin and n 21 for placebo in the primary summary. It does not explain why those outcome denominators are as listed, whether participants were excluded from particular analyses, or how missing measurements were handled. The registry does not state whether the primary comparison followed an intention-to-treat population, a per-protocol population, or another defined population.

These details matter because estimates can depend on who is included and how unavailable outcomes are treated. A complete-case analysis, for example, may describe only participants with recorded outcomes; other approaches make different assumptions about missing measurements. This is general methodological context, not a claim about the method used in this trial. Without the registry’s analysis-population and missing-data details, the extent to which the posted summaries represent all randomized participants cannot be determined.

The registry record also does not report the original sample-size rationale or the protocol’s planned statistical procedures. The planning illustrations based on observed effects do not recover that information. These reporting gaps constrain assessment of prespecification, multiplicity, and possible selection among analyses, but they do not by themselves demonstrate that any particular analysis was conducted improperly.

15. 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 0% reporting threshold.

The adverse-event record lists zero serious adverse events in the rifaximin group among 20 participants at risk and zero in the placebo group among 21 participants at risk. It also lists zero other adverse events in each group among the participants at risk. These are the figures recorded for the listed groups; they should not be interpreted as proof that no adverse events occurred outside the registry’s reported categories or collection period.

Deaths are not reported in the registry record. The record does not provide serious adverse-event descriptions, event timing, severity details beyond the serious classification, or information about how adverse events were collected. It also does not state whether participants who did not contribute to the outcome summaries were included in safety follow-up. With these reporting limits, the figures describe the registry’s posted safety counts but do not provide a complete account of safety monitoring or all possible harms.

Zero reported events in these groups is a count, not evidence that the underlying risk is zero. Safety estimates based on limited group sizes can remain uncertain, especially for uncommon events. The registry does not provide a separate statistical comparison for adverse events.

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

The posted primary result describes baseline GSRS scores in the two randomized groups. It does not estimate symptom relief after rifaximin because the registry identifies the primary measurement as occurring at week 0 and does not post a follow-up primary GSRS result. The point estimate and interval characterize a baseline comparison; they should not be presented as evidence that treatment did or did not change symptoms.

The registry also posts an abnormal breath-test outcome assessed up to 12 weeks. That measure is relevant to the study’s stated interest in breath-test results, but it is distinct from a symptom score. Its uncertainty and secondary status limit the strength of any broad conclusion drawn from it. The record does not provide reported analyses that would add detail about the analysis plan or the handling of missing outcome data.

More generally, a p-value is not a verdict on whether a treatment works, and a confidence interval is not proof of a particular effect. Estimates should be read in light of outcome timing, precision, analysis methods, and the clinical meaning of the measure. The registry does not report a threshold for a meaningful GSRS difference, nor does it provide the post-treatment primary symptom result needed to assess symptom change.

The findings therefore support a narrow description of the posted data: baseline symptom-score summaries and a secondary breath-test comparison are available, with uncertainty around the comparisons. They do not establish what happened to symptoms after treatment or provide a complete basis for evaluating the study’s stated symptom-relief question. This interpretation concerns the limits of the registry record and is not medical advice.

17. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation must begin with the outcome’s timing and definition. A study may be described as testing symptom relief, but the listed primary outcome is a baseline symptom score. Recognizing that distinction prevents a starting-value comparison from being mistaken for a treatment effect. The endpoint label, measurement time, and available results all matter when deciding what an estimate means.

The record also shows why estimates should be read with their confidence intervals rather than by point estimates or p-values alone. The primary comparison’s interval includes zero and spans differences in both directions. That uncertainty remains important even though the group means are close. A p-value does not indicate the probability that a treatment effect exists, and neither statistic supplies a clinical-importance threshold that the registry does not report.

Small outcome groups and limited event counts can leave comparisons imprecise. The planning illustrations make another statistical point: calculations based on observed effects can imply very different sample-size needs depending on the effect targeted. They are useful for understanding design trade-offs, but they do not reveal the assumptions used to design this trial and should not be mistaken for observed power.

Finally, missing reporting about the analysis plan, multiplicity, missing data, and analysis populations limits reproducibility and assessment of bias. These are not merely technical details: they help readers determine whether the reported comparisons were planned, who contributed data, and how uncertainty was handled. This record is a useful example of why outcome definitions and transparent analysis documentation are essential to interpreting clinical trial results.

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.

A central limitation is that the posted primary GSRS outcome is measured at baseline. The registry does not report a post-treatment primary symptom score or a change-from-baseline analysis, so the stated question about symptom relief cannot be answered from the primary result as listed. This limitation is specific to the mismatch between the study objective and the timing of the posted primary measure.

The registry reports outcome denominators of n 20 and n 21 for the primary summaries, while enrollment is listed as 50. It does not explain the denominators or provide a participant-flow account. The reason for the difference between enrollment and the outcome denominators is not reported in the registry record. The populations contributing to the breath-test outcome and the handling of missing observations are also not described in detail.

The breath-test outcome is the only posted secondary endpoint, and no reported secondary analyses are listed. The registry does not report a multiplicity plan, a detailed statistical analysis plan, or interim-analysis procedures. This limits the ability to assess whether the posted comparisons were prespecified and how multiple outcomes were considered.

The group summaries do not provide individual-level data, distributions, or information about adherence. The registry does not report eligibility criteria beyond the description of persistent symptoms despite a gluten-free diet, nor does it report a threshold for a clinically important GSRS difference. Safety counts are limited to the listed categories; deaths are not reported in the registry record. These omissions restrict interpretation without establishing that any particular unreported procedure or event occurred.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Rifaximin for the Treatment of Persistent Symptoms in Patients With Celiac Disease — NCT01137955.
• Registry record last updated 2022-06-29; status last verified 2022-06.
• Results first posted 2022-06-29.
• 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

The registry describes a completed, randomized, triple-masked, parallel-group trial sponsored by Columbia University. It lists enrollment of 50 and compares rifaximin, described as 400 mg three times a day for 10 days, with placebo pills given on the same schedule. The population of interest was patients with celiac disease and persistent symptoms despite a gluten-free diet.

The primary outcome is baseline GSRS score at week 0. The posted comparison summarizes starting scores and does not provide a post-treatment primary symptom result. One secondary outcome, abnormal breath-test status up to 12 weeks, is listed. The record does not report a detailed analysis plan, missing-data methods, analysis populations, or a multiplicity strategy. The available results should therefore be interpreted according to their endpoint timing and with attention to uncertainty and reporting gaps.