Safety and Effectiveness of 3 Doses of Crofelemer Compared to Placebo in the Treatment of HIV Associated Diarrhea: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Effectiveness of 3 Doses of Crofelemer Compared to Placebo in the Treatment of HIV Associated Diarrhea (NCT00547898), a randomized phase 3 study. The primary outcome is Primary Efficacy Outcome is Count of Participants With Two or Less Watery Bowel Movements Per Week During at Least Two Weeks of the Treatment Phase of the Optimal Dose of Crofelemer Compared to Placebo.

2. Clinical Question

The registry describes a two-stage study. Its brief summary says the first stage would determine an optimal dose using safety and response to therapy, and the second stage would further evaluate the effectiveness of that dose. The posted primary outcome analysis is limited to the selected dose and placebo. The other crofelemer doses are not included in that primary comparison because the record says they were not selected as optimal. This means the primary result answers a narrower question than a comparison of all three doses with placebo. It is a comparison of the selected dose with placebo using the stated binary response criterion, rather than a complete account of every dose or every possible diarrhea outcome.

3. Trial Design

The registry identifies this as a Phase 3 randomized, quadruple-masked, parallel-group trial with placebo control. The official title describes an orally administered, twice-daily regimen and a two-stage design. The brief summary characterizes the study as multicenter. The start is recorded as 2007-10, primary completion as 2011-01-27, and status as completed. Enrollment is listed as 374.

Four intervention groups are recorded: crofelemer 125 mg, 250 mg, and 500 mg, and placebo. The posted primary efficacy analysis does not compare all four groups. It compares crofelemer 125 mg twice daily with placebo twice daily. The registry states that the 125 mg group was selected as the optimal dose and that the other crofelemer doses were therefore not included in this analysis. The analysis-arm counts are 136 for crofelemer 125 mg and 138 for placebo.

Random allocation and masking are design features intended to limit systematic differences and influence in treatment assignment and outcome assessment. In general, a parallel-group design assigns participants to a group and compares outcomes across groups. The record does not report the randomization method, allocation concealment procedures, details of who was masked, or whether masking was maintained throughout the study. The original statistical analysis plan and the study's own sample-size justification are not reported in the registry record.

The registry lists two outcome measures but no posted secondary analyses. It reports one primary binary outcome analysis, expressed as counts of participants meeting a response criterion. The record does not provide a detailed account of the two-stage decision process, the timing of dose selection, or how the stage-specific data contributed to the final primary comparison.

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

Analysis population for the primary outcome, as defined in the registry: The primary efficacy analysis was pre-specified to be for the optimal dose of crofelemer compared to placebo. Crofelemer 125 mg BID group was selected as the optimal dose. Since other doses of crofelemer were not considered to be the optimal dose, they are not included in the analysis.

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 Primary Efficacy Outcome is Count of Participants With Two or Less Watery Bowel Movements Per Week During at Least Two Weeks of the Treatment Phase of the Optimal Dose of Crofelemer Compared to Placebo, measured over 31 days.

The primary endpoint counts participants who had two or fewer watery bowel movements per week during at least two weeks of the treatment phase. The registry gives the timeframe as 31 days and identifies the outcome unit as participants. It is therefore a binary response measure: each participant either met the stated criterion or did not, according to the endpoint definition. The posted results count 24 participants in the crofelemer 125 mg group and 11 in the placebo group as meeting it.

A threshold-based endpoint can make a treatment response easier to interpret as the proportion of participants reaching a specified level of symptom control, rather than as a change in an average bowel-movement count. Requiring the criterion during at least two weeks also makes the endpoint reflect repeated achievement during the treatment phase, rather than a single qualifying week. These are general features of this kind of endpoint; they do not establish how the criterion was selected or validated in this trial. The rationale for choosing this particular threshold and duration is not reported in the registry record.

The endpoint is narrower than the broader concepts of diarrhea severity, symptom burden, or quality of life. It does not, by itself, describe the frequency or duration of symptoms among participants who did not meet the response threshold. The registry does not report further details about endpoint assessment, diary completion, or handling of missing observations.

7. Results Posted in the Registry

• Crofelemer 125Mg BID: 17.6% (24/136) versus 8.0% (11/138) on control; risk difference 9.7 percentage points (95% CI 1.8 to 17.5), risk ratio 2.21 (1.13–4.34); unadjusted two-proportion z-test p = 0.016.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: participants are counted according to whether they met the criterion of two or fewer watery bowel movements per week during at least two weeks of the 31-day treatment phase. For a binary endpoint, group results can be described as event counts and proportions. Here, the registry lists 24 participants meeting the criterion among 136 in the crofelemer 125 mg group and 11 among 138 in the placebo group. The comparison statistics use those group summaries.

What does the risk difference mean?

The risk difference compares the proportion meeting the endpoint in one group with the corresponding proportion in the other. It is an absolute measure, expressed on the same proportion scale as the outcome. The reported estimate is 0.097, with a confidence interval from 0.018 to 0.175. In general, absolute measures are useful because they retain the outcome's underlying scale: the estimate describes the separation between the proportions, rather than expressing one group as a multiple of the other.

The risk ratio and odds ratio are relative measures. The reported risk ratio is 2.214, with confidence limits 1.129 and 4.34. The reported odds ratio is 2.474, with confidence limits 1.16 and 5.277. A risk ratio compares proportions directly; an odds ratio compares event odds. In general, odds and probabilities are different quantities, and an odds ratio should not be interpreted as if it were a risk ratio. Both relative measures depend on the event frequency in the groups, so it is useful to consider them alongside the absolute risk difference and the actual group proportions.

How should the p-value be understood?

The posted unadjusted p-value is 0.016. In general, a p-value measures how compatible the observed data are with a specified null model, assuming that model and the test assumptions hold. It is not the probability that the null model is true, nor does it convey the size of the observed difference. The registry does not report the statistical test used to obtain this p-value, so its exact test specification cannot be described from the record. The value is labeled unadjusted; no multiplicity adjustment is reported.

Randomization can support a causal comparison by making treatment groups comparable on average, but the validity of the inference also depends on trial conduct, outcome measurement, analysis choices, and missing data. The registry identifies the study as randomized, but does not report the randomization sequence method or allocation concealment. The record describes masking as quadruple but does not specify the roles of the masked parties or provide further implementation details.

Why does over-dispersion matter for some outcomes?

Over-dispersion is a general issue for count data when variability exceeds what a simple model expects. It can make standard errors too small if not handled appropriately. It is not the defining concern for the posted primary analysis because that result is recorded as a binary count of participants meeting a criterion, not as a model of a continuous count of bowel movements. No dispersion estimate or model-based adjustment is reported for this endpoint.

The registry says the study used two stages: an initial stage to select an optimal dose based on safety and response, followed by further evaluation of that dose. Selection among doses can affect how a final comparison should be interpreted, particularly if selection and evaluation use overlapping information. The record does not provide enough detail to determine how the stages were conducted analytically, whether the stages were combined, or how dose-selection uncertainty was handled. It is therefore not appropriate to assume a particular adjustment or independent validation step.

The primary analysis population is not described in detail. The record gives group counts for the outcome comparison but does not say whether it used an intention-to-treat, per-protocol, or another population definition. It also does not describe outcome-data completeness or imputation. In general, missing outcomes can affect binary response estimates when the likelihood of missingness differs across groups or relates to response. Without the registry's missing-data method and population definition, the direction or size of any such effect cannot be assessed.

The registry lists two outcome measures, while the posted analysis count is zero and no secondary analyses are posted. The record does not state how the primary outcome was prioritized relative to other outcomes, whether additional statistical tests were conducted, or how multiplicity was handled. These details matter because testing several outcomes, doses, or subgroups can increase the chance of a nominally unusual result. The available record does not permit a judgment about the extent of such testing.

Overall, the displayed comparison is an unadjusted comparison of the posted group summaries, and the record marks no discrepancy between the posted estimate and the recalculation. That agreement supports describing the arithmetic of the posted summary, but it does not replace information about the trial's prespecified statistical plan, analysis population, or missing-data handling. Those aspects are not reported in the registry record.

10. Confidence Intervals and Precision

The risk-difference estimate is 0.097, and its confidence interval extends from 0.018 to 0.175. A confidence interval is a range produced by a statistical procedure that, under its assumptions, reflects the uncertainty associated with an estimate. It is not a range that guarantees the true effect lies within it, nor does it describe the spread of individual participant outcomes. The width of an interval depends on the data and the method used.

For this comparison, the interval's lower and upper limits are above zero. This indicates that the interval from the reported procedure does not include no difference on the risk-difference scale. The interval still covers a range of possible effect sizes, so the point estimate should not be treated as exact. The unadjusted p-value is 0.016, but the registry does not report the test details or whether the interval and p-value use exactly aligned procedures.

The relative-effect intervals are also reported: the risk ratio is 2.214, with limits 1.129 and 4.34, and the odds ratio is 2.474, with limits 1.16 and 5.277. Their scales differ from the risk difference, and their intervals should be interpreted on their respective scales. None of these intervals accounts for sources of uncertainty that are not represented by the statistical calculation, such as uncertainty from dose selection, missing data, or unreported analysis decisions.

The estimate is based on the two groups included in the primary comparison. The other crofelemer doses are excluded from that analysis, and the registry does not report a separate precision estimate for them. The confidence intervals therefore should not be read as addressing the full range of dose comparisons or all trial outcomes.

11. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed risk difference, not the trial's original design calculation. For this binary outcome, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The registry's original sample-size assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm used in the planning calculation to provide an 80% chance of detecting the specified effect under those assumptions, if that effect is present. The 90% power column describes the corresponding planning number for a 90% chance. These are design probabilities under the calculation's assumptions, not guarantees about the outcome of a future study. They are not observed power.

The rows use the full observed effect and smaller fractions of that effect. Planning for 75% of the observed effect requires more participants per arm than planning for the full observed effect; planning for 50% requires more again. In general, smaller effects are harder to distinguish from random variation at a fixed significance level and power target, so they require larger planned groups under otherwise unchanged assumptions.

The values are hypothetical planning illustrations, not evidence that a study with those group sizes would reproduce this trial's result. They do not account for details absent from the planning assumptions, such as the original two-stage design, dose selection, missing outcomes, or multiplicity. The accompanying curve should be read in the same planning context: it represents how the illustrative participant requirement changes with the effect size used in the calculation, not an observed trial outcome.

12. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.080; treatment proportion p₁ = 0.176; average p̄ = 0.128.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4726 = 0.9263.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4676 = 0.3936.
4. n = (0.9263 + 0.3936)² / (0.0968)² = 186.1, rounded up to 187 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 <- 0.0797101449275362                          # control proportion
p1 <- 0.176470588235294                          # 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(547898)
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 = 187 (80% power), 249 (90% power)
 75% of observed effect: n per arm = 305 (80% power), 408 (90% power)
 50% of observed effect: n per arm = 624 (80% power), 834 (90% power)
power.prop.test: 186.1 
Simulated power at n = 187 per arm: 0.810 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns arise when several hypotheses, outcomes, doses, timepoints, or subgroups are examined. The registry lists two outcome measures, but the posted analysis count is zero and no secondary analyses are posted. It does not report whether additional comparisons were conducted, whether a primary testing sequence was defined, or whether the reported unadjusted p-value was adjusted for multiple testing. A multiplicity strategy is therefore not reported in the registry record.

The study included three crofelemer doses, and the registry describes a two-stage process in which an optimal dose was selected based on safety and response before further evaluation. The 125 mg twice-daily dose was selected as optimal and is the only crofelemer dose in the posted primary comparison. The record does not explain the dose-selection criteria in detail or how the selection process was reflected in the uncertainty estimates and hypothesis testing. Because selection among doses can influence interpretation, this missing information is relevant when considering the unadjusted result.

The analysis population is not specified beyond the group counts reported for the primary endpoint. The registry does not say whether all randomized participants were included, how participants were handled if they discontinued, or whether the analysis followed an intention-to-treat or per-protocol principle. The number of participants with missing endpoint data and the reasons for any missingness are not reported in the registry record.

No missing-data procedure is described. The record does not state whether missing endpoint observations were excluded, imputed, or classified in another way. In general, missing data can affect a treatment comparison if missingness is related to group assignment or the chance of meeting the response criterion. Without information on completeness and handling, the potential impact cannot be assessed.

These gaps do not change the counts and comparison statistics posted in the registry, but they limit assessment of how the primary analysis was specified and how robust it is to analysis choices. The original statistical plan, multiplicity approach, population definition, and missing-data handling are not reported in the registry record.

14. 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

Serious events with the highest arm-level rate: escherichia sepsis (0.8%), pneumonia (0.8%), pancreatitis acute (0.7%), diffuse large b-cell lymphoma (0.7%), alcohol withdrawal syndrome (0.7%).

The serious adverse event summary reports 4 affected participants among 137 at risk in the placebo group and 2 among 130 at risk in the crofelemer 125 mg group. For crofelemer 250 mg, the record reports 0 among 54 at risk; for crofelemer 500 mg, it reports 0 among 42 at risk. These are serious adverse event figures for the listed groups, not the primary efficacy outcome. The group counts at risk in this safety summary need not match the efficacy-analysis counts.

The registry's summary for other adverse events reports 0 affected participants in each listed group. A zero in this posted summary means that no affected participants are recorded for that category in the displayed figures; it does not establish that no events of any kind occurred or that rare events are ruled out. The record lists serious-event terms including ESCHERICHIA SEPSIS and PNEUMONIA at 0.8%, and PANCREATITIS ACUTE, DIFFUSE LARGE B-CELL LYMPHOMA, and ALCOHOL WITHDRAWAL SYNDROME at 0.7%. These terms are reported as registry entries; the record does not provide further context for interpreting their relationship to treatment.

Deaths are not reported in the registry record. These summaries alone do not establish comparative safety, and they do not replace a full safety assessment with event definitions, timing, severity, relatedness, and follow-up information.

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

The posted result describes a difference between the crofelemer 125 mg twice-daily group and the placebo group on a specific response criterion during a 31-day treatment phase. The observed counts were 24 of 136 and 11 of 138, respectively. The risk-difference estimate was 0.097, with a confidence interval from 0.018 to 0.175, and the unadjusted p-value was 0.016. Those numbers summarize the trial's reported primary comparison; they do not, on their own, answer every question about diarrhea symptoms or treatment outcomes.

The endpoint counts participants who achieved two or fewer watery bowel movements per week during at least two weeks. It does not describe the full range of symptom changes, the number of bowel movements among those who did not meet the criterion, or longer-term outcomes. The registry does not report the endpoint's rationale, further follow-up results, or a detailed account of how missing observations were handled.

The result applies to the selected 125 mg dose comparison presented in the registry. It should not be generalized as a comparison of every crofelemer dose: the 250 mg and 500 mg groups are not included in the primary efficacy analysis. The record also does not provide enough detail to evaluate the two-stage dose-selection process or its effect on inference. The reported confidence interval captures statistical uncertainty under its method, but not necessarily uncertainty from those unreported design and analysis details.

A group comparison is not an individual prediction. The result does not indicate which particular participant would meet the endpoint, nor does it establish the likelihood of response for people outside the study population. The registry record does not report detailed participant characteristics that would support assessing how closely the study groups represent other populations.

The safety figures are separate from the efficacy result. They report serious adverse events and other adverse events in the listed groups, but do not provide a complete safety narrative or deaths. The posted statistics should therefore be read as specific summaries of the recorded outcomes, not as a comprehensive determination of benefit, harm, or the result's broader clinical meaning.

16. Why This Trial Matters Statistically

This trial raises a statistical issue common to multi-dose studies: the primary comparison concerns a dose selected through a stated two-stage process, rather than a dose fixed in isolation from the study's dose-selection objective. The record says that crofelemer 125 mg twice daily was selected as optimal based on safety and response, then identifies that dose as the one used in the primary efficacy analysis. Understanding how selection was incorporated into the analysis is important because choosing among alternatives can influence the interpretation of an estimated effect and its uncertainty. The registry does not report those analytic details.

The result also illustrates why effect measures should be read on more than one scale. The reported risk difference of 0.097 expresses an absolute separation in the observed response proportions, while the risk ratio and odds ratio express relative comparisons. The confidence interval helps show uncertainty around the risk-difference estimate, and the unadjusted p-value addresses compatibility with a null model rather than clinical importance. Keeping these concepts separate prevents a p-value or relative measure from standing in for the full result.

The binary endpoint makes a repeated symptom threshold interpretable as a participant-level response, but it also compresses varied symptom experiences into a yes-or-no classification. The endpoint does not describe how far a participant was from meeting the criterion or the distribution of symptom changes. It is therefore useful to interpret the statistical comparison alongside the precise endpoint definition.

Finally, the record's limitations are themselves relevant to statistical reading. The analysis population, missing-data method, multiplicity approach, and original design assumptions are not reported in the registry record. Those details affect how readers assess robustness and reproducibility. The posted summaries allow a focused reading of the primary comparison, while leaving important aspects of the analysis process unresolved.

17. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record provides a focused primary comparison but leaves several trial-specific details unresolved. Although it describes a randomized, quadruple-masked, two-stage, parallel-group study, it does not report the randomization method, allocation concealment procedures, the parties covered by masking, or details of how masking was maintained. It also does not provide a fuller account of the stage transition or the rules used to select the optimal dose.

The primary analysis is restricted to crofelemer 125 mg twice daily versus placebo. The 250 mg and 500 mg groups are not included because the registry identifies 125 mg as the selected optimal dose. The record does not explain whether dose selection and the final efficacy comparison used independent data or how selection was accounted for statistically. This limits interpretation of the confidence interval and p-value as measures of uncertainty for the overall dose-selection process.

The population definition for the primary analysis is not reported in the registry record. The efficacy counts are listed, but the record does not describe participant exclusions, endpoint completeness, or missing-data handling. It does not report the reason for the selected response threshold or details of the instrument or procedure used to assess watery bowel movements. The clinical characteristics of participants are also not presented in the record excerpt.

The registry lists two outcome measures but posts no secondary analyses. It does not describe a multiplicity plan, a prespecified analysis plan, or the original sample-size justification. The two-stage design's implications for hypothesis testing are therefore not assessable from the available record. Safety information is also limited to the posted event summaries; deaths are not reported in the registry record, and the summary does not provide detailed timing or attribution information.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Safety and Effectiveness of 3 Doses of Crofelemer Compared to Placebo in the Treatment of HIV Associated Diarrhea — NCT00547898.
• Registry record last updated 2020-09-03; status last verified 2020-08.
• Results first posted 2020-09-03.
• 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.

21. Record Summary

The registry identifies NCT00547898 as a completed Phase 3 randomized, quadruple-masked, parallel-group, placebo-controlled study of crofelemer for HIV-associated diarrhea. Enrollment is listed as 374. The record gives a start of 2007-10 and a primary completion date of 2011-01-27.

The study included crofelemer 125 mg, 250 mg, and 500 mg, as well as placebo. The posted primary efficacy comparison is crofelemer 125 mg twice daily versus placebo. Its endpoint counted participants with two or fewer watery bowel movements per week during at least two weeks of the 31-day treatment phase. The reported counts were 24 of 136 and 11 of 138, with a risk difference of 0.097 and confidence interval from 0.018 to 0.175; the unadjusted p-value was 0.016.

The registry describes a two-stage study and identifies the 125 mg dose as the selected optimal dose. It does not report the original statistical plan, population definition, missing-data method, multiplicity approach, or deaths. The posted result is therefore best understood as a specific comparison for the stated endpoint, alongside the limits of the available record.