PAR-101/OPT-80 Versus Vancomycin for the Treatment of Clostridium Difficile-Associated Diarrhea (CDAD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for PAR-101/OPT-80 Versus Vancomycin for the Treatment of Clostridium Difficile-Associated Diarrhea (CDAD) (NCT00468728), a randomized phase 3 study. The primary outcome is Cure Rate at End of Therapy.

2. Clinical Question

The cure definition required 3 or fewer unformed stools for 2 consecutive days, with that condition maintained through the end of therapy. It also required that the participant no longer needed specific anti-Clostridium antibacterial treatment after completing the study medication course. The trial additionally reported recurrence during Study days 11-40 and global cure at the end of the study.

The primary question is about a binary outcome: each participant either met the stated cure criteria or did not. The registry reports the percentage meeting those criteria in each group and a comparison between groups. This makes the result interpretable as a comparison of observed proportions, while leaving the uncertainty around that comparison important to the conclusion. The registry record identifies the primary analysis population and endpoint timeframe, but the original protocol’s full statistical assumptions and the clinical threshold used for any non-inferiority or equivalence conclusion are not reported in the registry record.

3. Trial Design

NCT00468728 is a completed Phase 3 randomized parallel-group study comparing PAR-101/OPT-80 with vancomycin in participants with CDAD. The registry lists quadruple masking. The enrollment field reports 535 participants. The listed interventions are both drugs, and the arm descriptions identify vancomycin and PAR-101/OPT-80 as the treatment groups.

The primary endpoint was the percentage of participants cured at the end of therapy, measured on Study day 10 (+/- 2 days). The registry defines the modified intent-to-treat population for this endpoint as participants with more than 3 unformed bowel movements in the 24 hours before randomization, a positive toxin assay, and at least one dose of study medication. The posted primary arm counts are 256 for vancomycin and 253 for PAR-101/OPT-80. Those are analysis counts; the registry’s overall enrollment field is a separate trial-level figure.

Two additional outcomes are posted: recurrence during Study days 11-40 and global cure at the end of the study. The registry lists 3 outcome measures and 3 analyses overall. It does not report the randomization ratio, the method used to generate or conceal the allocation sequence, or the original design assumptions for sample size. Those details should not be inferred from the observed group counts or from the planning illustrations based on the observed results.

The registry gives a start date of 2006-10-04, a primary completion date of 2009-12-11, and a completed status. The sponsor is Optimer Pharmaceuticals LLC, a subsidiary of Merck & Co., Inc. (Rahway, New Jersey USA). These are record characteristics; they do not by themselves describe how the analysis was conducted or establish the validity of any particular statistical conclusion.

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.

Enrollment

Treatment

Reasons for not completing this period:

Follow-up

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis data is modified intent to treat (mITT) population. The mITT population consists of subjects that had CDAD confirmed by \>3 unformed bowel movements in the 24 hours prior to randomization and a positive toxin assay and received at least one dose of study medication.

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 Cure Rate at End of Therapy, measured over Study day 10 (+/- 2 days).

The primary endpoint is the percentage of participants who met the registry’s definition of cure at the end of therapy. Cure required 3 or fewer unformed stools for 2 consecutive days, maintained through the end of therapy, and no continued need for specific anti-Clostridium antibacterial treatment after the study medication course. The assessment timeframe was Study day 10 (+/- 2 days).

This endpoint is useful because it combines a symptom-based criterion with a treatment-use criterion at a prespecified point near the end of therapy. As a binary outcome, it allows the result to be expressed as the percentage meeting the definition in each group and as a between-group risk difference. These measures describe how common the defined outcome was in the analyzed participants. They do not capture every aspect of the illness or recovery, and a percentage alone does not show how precisely the treatment groups differ.

The primary analysis population was modified intent-to-treat. It included participants with CDAD confirmed by more than 3 unformed bowel movements in the 24 hours before randomization and a positive toxin assay, provided they received at least one dose of study medication. The registry record describes these criteria, but does not report the full protocol for handling missing endpoint observations. The result therefore needs to be read in the context of the specified analysis population and the uncertainty around the group comparison, rather than as a complete account of every participant’s clinical course.

7. Results Posted in the Registry

• PAR-101/OPT-80: 87.7% (222/253) versus 86.7% (222/256) on control; risk difference 1.0 percentage points (95% CI -4.8 to 6.8), risk ratio 1.01 (0.95–1.08); unadjusted two-proportion z-test p = 0.728.

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.

Recurrence

• 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:
  • PAR-101/OPT-80: 12.6% (28/222) versus 27.0% (60/222) on control; risk difference -14.4 percentage points (95% CI -21.7 to -7.1), risk ratio 0.47 (0.31–0.70); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for PAR-101/OPT-80 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Global Cure

• 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:
  • PAR-101/OPT-80: 76.7% (194/253) versus 63.3% (162/256) on control; risk difference 13.4 percentage points (95% CI 5.5 to 21.3), risk ratio 1.21 (1.08–1.36); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for PAR-101/OPT-80 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the two secondary outcomes, the posted comparisons point in the same general direction: the estimates favor PAR-101/OPT-80. The outcomes extend the assessment beyond cure at end of therapy, covering recurrence during Study days 11-40 and global cure at the end of the study. These measures are related to the primary endpoint but represent different events and timepoints, so they add context rather than serving as interchangeable confirmations of the primary result.

The registry reports unadjusted analyses for both secondary outcomes. No multiplicity plan or adjustment is reported in the registry record. When multiple outcomes are examined, the chance of seeing at least one result that appears statistically notable can increase, even if there is no corresponding underlying difference. For that reason, the secondary results should generally carry less evidential weight than a clearly specified primary analysis, particularly when the registry does not state how the set of outcomes was handled statistically.

Directionally aligned outcomes can be informative, especially when the outcomes describe distinct but related aspects of the study question. However, their interpretation still depends on the definitions, analysis populations, timeframes, and uncertainty for each outcome. They do not resolve the primary endpoint’s uncertainty or establish a non-inferiority or equivalence conclusion without a reported margin. Nor does their pattern alone establish a broader treatment effect beyond the particular registry outcomes.

It is also important that the analyses have different denominators and definitions. Recurrence is assessed among participants represented in its posted analysis, whereas global cure uses a different endpoint and timeframe. These distinctions affect what each comparison means. The posted pattern is therefore best treated as supportive descriptive evidence subject to the limitations of unadjusted multiple outcome testing, rather than as a single combined result.

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

• Recurrence
• Global Cure

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: a participant either met the registry’s cure criteria or did not. For this type of outcome, the proportion is the number of participants with the event divided by the number analyzed in that group. The registry reports the resulting percentages and 95% confidence intervals for each arm. The between-group risk difference expresses the difference in those proportions. In the reported primary comparison, the sponsor states the risk difference in percentage points.

What does a risk difference describe?

A risk difference compares the event proportions directly by subtracting one group’s proportion from the other’s. A value near zero indicates that the observed proportions are close. A positive or negative value indicates which group had the higher observed proportion, according to the comparison’s ordering. The estimate is a sample result, so it is interpreted alongside its confidence interval. The registry also includes recalculated risk ratios and odds ratios for some comparisons; these use different scales and answer related, but not identical, questions. The risk ratio compares proportions as a ratio, while the odds ratio compares event odds. Neither measure replaces the directly interpretable percentage-point comparison.

How should a confidence interval be read?

A confidence interval gives a range of values compatible with the data and the method used, at the stated confidence level. Wider intervals indicate less precision; narrower intervals indicate more precision. For a risk difference, an interval crossing zero includes no difference as one value compatible with the data. It may also include values in both directions. The interval does not assign a probability to the true effect being in that particular range, and it does not account for design or analysis limitations that are not represented in the calculation.

The primary sponsor analysis reports a 95% confidence interval for the risk difference. The registry categorizes that analysis as non-inferiority or equivalence, but a non-inferiority or equivalence interpretation requires a margin that defines how large a difference is acceptable for the stated purpose. That margin is not reported in the registry record. A confidence interval cannot be evaluated against an unreported threshold, so the label alone does not supply the missing statistical criterion.

What does an unadjusted p-value mean?

A p-value measures how inconsistent the observed data are with a specified null hypothesis under the statistical method used. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The recalculated primary comparison has an unadjusted p-value of 0.728. That value is not a substitute for the confidence interval or the sponsor’s analysis. It also does not establish equivalence: failure to reject a no-difference hypothesis is not the same as demonstrating that differences are confined within an acceptable margin.

For the secondary outcomes, the registry reports Chi-squared methods and p-values. A Chi-squared test compares observed event counts with counts expected under a null hypothesis of no association between group and outcome. Its interpretation depends on the data and assumptions, and the registry does not report additional details about implementation. The secondary p-values are unadjusted in the posted analyses. When several outcomes are tested, multiplicity is a concern because the more tests performed, the greater the chance of at least one apparently small p-value under repeated testing. The registry’s approach to controlling that risk is not reported in the registry record.

Why can over-dispersion matter?

Over-dispersion is a general statistical concern when variability in data exceeds what a model assumes. It can lead to uncertainty being understated if the analysis does not account for the extra variability. The posted primary outcome is a binary percentage, and the registry does not report an over-dispersion adjustment. This concept should not be taken to mean that over-dispersion was present in this trial; it illustrates why model assumptions and analysis details matter when interpreting estimates.

The analysis population is also central. The primary endpoint uses a modified intent-to-treat population, with the registry specifying confirmation criteria and at least one dose. The posted denominators differ from the trial-level enrollment figure, as is possible when an endpoint is analyzed in a defined population. The registry record does not report enough information to reconstruct every participant’s disposition or determine how missing primary outcome observations were handled. These gaps limit what can be concluded about the sensitivity of the result to exclusions or missingness.

11. Confidence Intervals and Precision

Precision is about how tightly the data estimate a group difference, rather than whether the point estimate is favorable to one group. The primary endpoint’s sponsor-reported risk difference is 1.0 percentage point, with a 95% confidence interval from -4.8 to 6.8. The interval includes zero and extends in both directions. Thus, the observed estimate is close to no difference, but the uncertainty also allows for a modest difference favoring either group on this scale.

The arm-level primary confidence intervals also convey uncertainty in each group’s cure percentage: 82.0 to 90.4 for vancomycin and 83.1 to 91.2 for PAR-101/OPT-80. These intervals are not themselves a direct test of the difference between groups. For a treatment comparison, the interval for the risk difference is the more direct summary because it estimates the between-group contrast.

Confidence intervals are affected by the number of observations and by the frequency of the outcome, as well as by the analysis method. The primary analysis counts are 256 for vancomycin and 253 for PAR-101/OPT-80. Those counts help place the interval in context, but the width should be interpreted from the posted interval rather than inferred from sample size alone. An interval is not a guarantee about the true effect and does not account for unreported choices such as missing-data handling or multiplicity.

For non-inferiority or equivalence, precision must be considered against an acceptable margin. Since that margin is not reported in the registry record, the primary interval cannot independently establish either conclusion. It does show that a range of possible risk differences remains compatible with the posted analysis. The distinctions between estimation, testing, and a margin-based conclusion are important: a near-zero point estimate is not, by itself, proof of equivalence.

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 figures are planning illustrations based on the observed effect, not the trial’s original design calculation. For binary outcomes, the displayed values are participants per arm, not total participants. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning scenario uses the stated fraction of the observed effect. The original trial’s own sample-size assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation would require to have an 80% chance of detecting the specified effect, under those assumptions. The 90% power column gives the corresponding number for a 90% chance. Power is a property of a planned design under specified assumptions; it is not a probability that a particular study result is correct. These figures are not observed power.

Rows that plan for a smaller fraction of the observed effect require more participants per arm. That is because a smaller difference is harder to distinguish from random variation under the same assumptions. The illustrations should be read as conditional planning scenarios, not recommendations or a reconstruction of the actual trial design. They also do not incorporate every possible design feature, analysis choice, missing-data issue, or multiplicity adjustment. The curve and values are best understood as showing how the assumed target effect and desired power relate to the required group size under the stated simplified planning approach.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.867; treatment proportion p₁ = 0.877; average p̄ = 0.872.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4720 = 0.9250.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4719 = 0.3972.
4. n = (0.9250 + 0.3972)² / (0.0103)² = 16,533.0, rounded up to 16,534 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 <- 0.8671875                          # control proportion
p1 <- 0.877470355731225                          # 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(468728)
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 = 16,534 (80% power), 22,133 (90% power)
 75% of observed effect: n per arm = 29,646 (80% power), 39,686 (90% power)
 50% of observed effect: n per arm = 67,269 (80% power), 90,053 (90% power)
power.prop.test: 16533 
Simulated power at n = 16,534 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary risk-difference estimate as 1.0, with a 95% confidence interval from -4.8 to 6.8, and labels the analysis as non-inferiority or equivalence. The recalculation from posted summary statistics is unadjusted and gives p = 0.728. The comparison is broadly consistent with the close observed arm percentages, but the sponsor’s own analysis takes precedence when discussing the sponsor-reported result.

The registry does not report a primary p-value, the method used for the sponsor’s primary analysis, or the margin required to assess a non-inferiority or equivalence claim. Therefore the recalculated p-value should not be used as if it were the sponsor’s prespecified test, and it does not supply the missing margin. The two analyses answer related questions but are not identical in purpose or necessarily in method.

For the secondary outcomes, the sponsor-reported analyses include Chi-squared methods and p-values. Their estimates and intervals are close to the unadjusted recalculations from posted summary statistics, with some differences in reported interval limits or rounding. These recalculations are simple unadjusted checks; they do not replace the sponsor’s analysis or account for any adjustments not described in the registry record. Where the sponsor’s analysis is reported, it remains the primary reference for the trial’s own stated analysis.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines more than one outcome, comparison, subgroup, or analysis and then interprets the resulting statistical tests. Even when each test uses the same nominal significance threshold, a larger family of tests creates more opportunities for at least one result to appear statistically significant by chance. A prespecified strategy can define which outcomes are primary, how secondary outcomes are tested, and whether adjustments are used to control error rates.

This registry record identifies a primary outcome and two secondary outcomes. It reports a primary analysis categorized as non-inferiority or equivalence and Chi-squared analyses for the secondary outcomes. However, the approach to multiplicity, including any testing hierarchy or adjustment, is not reported in the registry record. The secondary analyses are unadjusted as posted. Their p-values should consequently be interpreted with care and should not be treated as though they were protected from repeated-testing concerns.

The record defines the primary modified intent-to-treat population and provides denominators for the reported outcomes. It does not report full participant flow, missing outcome counts, or the method used to handle missing observations. It is therefore not possible to determine from the registry record whether missing data were absent, excluded, imputed, or addressed through another strategy. Missingness can affect interpretation if the probability of having an observed outcome differs across groups or is related to the outcome itself; this is a general concern, not evidence that such a pattern occurred in this trial.

The registry also does not report a complete statistical analysis plan, the original sample-size justification, or the non-inferiority/equivalence margin. These omissions matter because they define how the primary claim should be tested and how the analysis was intended to control uncertainty. The posted numbers remain interpretable as reported outcome estimates, but the absence of those details limits assessment of whether all analysis decisions followed a prespecified plan and whether the uncertainty statements cover the full set of analyses.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (1.9%), clostridium difficile colitis (1.9%), neutropenia (1.5%), myocardial infarction (1.5%), sepsis (1.5%).

The registry reports serious adverse event counts among 260 participants at risk in the vancomycin group and 264 at risk in the PAR-101/OPT-80 group. The corresponding numbers affected were 58 and 70. It also reports other adverse event counts of 177 among 260 at risk for vancomycin and 186 among 264 at risk for PAR-101/OPT-80. These are descriptive counts with the listed at-risk denominators; they should not be treated as causal comparisons by themselves.

The record lists pneumonia and Clostridium difficile colitis at 1.9% each among the top serious terms, and neutropenia, myocardial infarction, sepsis, and hyponatraemia at 1.5% each. These terms describe reported events; the record does not establish that the study medication caused them. Death counts are not reported in the registry record.

Safety comparisons require attention to event definitions, exposure duration, ascertainment, and uncertainty. The registry summary does not provide enough detail to determine how events were judged for relatedness or whether exposure differed between groups. Counts alone do not show severity distributions, timing, or the full clinical context. The posted figures are therefore best read as a summary of reported adverse events, not as a complete comparative safety assessment.

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

The primary result describes end-of-therapy cure under the registry’s definition and in its modified intent-to-treat population. The observed percentages are close, and the sponsor-reported risk-difference interval includes zero while spanning values on both sides. This means the estimate is not precise enough to rule out every potentially relevant difference in either direction on the reported scale. It does not establish that the treatments are identical.

The registry classifies the primary analysis as non-inferiority or equivalence, but the margin needed to interpret such a conclusion is not reported in the registry record. A near-zero point estimate and a confidence interval that includes zero do not, on their own, demonstrate non-inferiority or equivalence. Those conclusions require a defined threshold and an analysis showing that the relevant interval satisfies it.

The secondary outcomes provide additional comparisons for recurrence and global cure. Their overall direction favors PAR-101/OPT-80, but the analyses are unadjusted and the registry’s multiplicity approach is not reported. They should therefore be interpreted as secondary evidence, not as a substitute for the primary endpoint or as conclusive proof of a broad effect.

These findings apply to the participants and endpoints represented in the registry record. The primary population required specified clinical and assay criteria and at least one dose of study medication. The registry does not report all details of missing-data handling, the original design assumptions, or the full statistical analysis plan. Those omissions constrain how confidently the estimates can be connected to a particular confirmatory claim.

The results do not establish the cause of adverse events, resolve unreported aspects of participant follow-up, or determine outcomes beyond the posted definitions and timeframes. They are estimates with uncertainty, not guarantees about an individual participant’s course. Their proper interpretation stays within the trial population, the recorded outcomes, and the statistical information available in the registry.

18. Why This Trial Matters Statistically

This trial illustrates why the interpretation of a close pair of percentages depends on more than the point estimates. The primary comparison includes an estimate and a confidence interval, and the interval is essential to understanding how much uncertainty remains. A small observed difference is not equivalent to precise evidence of no meaningful difference.

It also highlights the distinction between superiority and non-inferiority or equivalence. A conventional test of no difference and a margin-based assessment answer different questions. A non-inferiority or equivalence claim needs a prespecified margin, and the registry record does not report one. The sponsor’s analysis category is informative about the intended type of claim, but does not provide enough detail to independently evaluate that claim.

The secondary outcomes show why multiplicity matters. Multiple related endpoints can provide a richer picture, but unadjusted tests increase the risk of overstating evidence if each result is treated as an independent confirmatory finding. Their consistent direction can be described, while still recognizing that the registry does not report a multiplicity strategy.

Finally, the sample-size illustrations emphasize that planning depends on the effect size a study aims to detect and the desired power. The planning figures are based on observed effects and simplified stated assumptions, not the trial’s original design. Reading them as a reconstruction of the actual protocol would confuse retrospective illustrations with prospective design choices. Together, these points make the trial useful for understanding estimation, confidence intervals, margin-based claims, secondary analyses, and the limits of registry-level statistical detail.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several trial-specific details needed for a full statistical appraisal are not reported in the registry record. The non-inferiority or equivalence margin for the primary analysis is absent, so the sponsor’s stated analysis category cannot be evaluated against a clinical or statistical threshold. The primary analysis method and its p-value are also not reported, making the sponsor result difficult to reproduce from the record alone.

The original sample-size justification and assumptions are not reported. The planning illustrations use observed effects and stated hypothetical assumptions, and therefore cannot establish what the trial was designed to detect. The randomization ratio and allocation-sequence details are likewise not reported in the registry record.

The record gives the primary modified intent-to-treat definition and outcome denominators, but does not provide full participant disposition or a missing-data strategy. That prevents assessment of how exclusions or missing endpoint observations may have affected the results. A multiplicity approach for the primary and secondary analyses is also not reported; the secondary p-values are unadjusted.

For safety, the summary gives event counts and selected serious event terms, but does not report deaths, detailed event timing, exposure-adjusted rates, or enough information about event attribution. These are limitations of the registry summary and should not be filled in by assumption. The record’s reported outcomes and estimates remain useful, but their scope is narrower than a complete trial report with protocol, analysis plan, participant flow, and detailed safety data.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: PAR-101/OPT-80 Versus Vancomycin for the Treatment of Clostridium Difficile-Associated Diarrhea (CDAD) — NCT00468728.
• Registry record last updated 2017-04-21; status last verified 2017-03.
• Results first posted 2011-07-29.
• 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.

23. Record Summary

NCT00468728 is a completed Phase 3 randomized, quadruple-masked, parallel-group study comparing PAR-101/OPT-80 with vancomycin for Clostridium difficile-associated diarrhea. The registry lists enrollment of 535. The primary endpoint was cure rate at end of therapy, measured on Study day 10 (+/- 2 days), in a modified intent-to-treat population.

The sponsor-reported primary risk difference was 1.0, with a 95% confidence interval from -4.8 to 6.8; the registry categorizes the analysis as non-inferiority or equivalence. The margin for that assessment is not reported in the registry record. The two posted secondary outcomes are recurrence and global cure, both with unadjusted analyses.

The record reports adverse event counts and selected serious adverse event terms, but does not report death counts. Important details—including the original sample-size assumptions, missing-data handling, and multiplicity plan—are not reported in the registry record. The results should be interpreted as estimates for the recorded populations, endpoints, and timeframes, with those limits in mind.