A Dose-finding Study of OPC-6535 in Patients With Active Crohn's Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Dose-finding Study of OPC-6535 in Patients With Active Crohn's Disease (NCT00317369), a randomized phase 2 study. The primary outcome is Clinical Improvement Rate (Number of Subjects Showing Clinical Improvement/Number of Subjects Evaluated x 100) After 8 Weeks of Study Drug Administration.

2. Clinical Question

3. Trial Design

This was a phase 2, randomized, double-masked, parallel-group study of OPC-6535 in patients with active Crohn's disease. The registry record lists 29 participants enrolled and identifies the status as terminated. The study start is recorded as 2006-05, and primary completion as 2007-07-11. The record does not report the reason for termination.

The study summary describes once-daily oral OPC-6535 at 0, 25, or 50 mg for 8 weeks. The primary outcome results identify the placebo, 25 mg, and 50 mg groups. The summary says treatment was combined with a fixed oral dose of 5-ASA or with a fixed oral dose of 5-ASA and enteral nutrition, but does not state how those background regimens were distributed across the groups.

The term randomized means allocation was described as random; double-masked means the study was described as double-blind, although the registry record does not provide operational details about masking. Parallel-group describes assignment to groups followed over the study period, rather than a planned crossover between treatments. These are general descriptions of the design terms, not additional details about how this trial was conducted.

The record does not report the randomization method, allocation concealment, masking procedures, protocol deviations, or the original sample-size justification. It also does not report a detailed statistical analysis plan or interim-analysis plan. The posted efficacy results include 10 participants for OPC-6535 25 mg, 9 for OPC-6535 50 mg, and 10 for placebo; these arm-specific endpoint counts sum to the recorded enrollment of 29, but the registry record does not explain participant flow or whether the counts apply to every outcome.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Efficacy was evaluated in the subjects who took at least one dose of the study drug and provided postdosing data concerning the efficacy endpoints. Subjects with GCP violations (noncompliance of obtaining informed consent, start of the trial before obtaining informed consent, trial conducted outside the contract period) were to be excluded from 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 Clinical Improvement Rate (Number of Subjects Showing Clinical Improvement/Number of Subjects Evaluated x 100) After 8 Weeks of Study Drug Administration, measured over Week 8.

The primary endpoint was the clinical improvement rate after 8 weeks of study drug administration: the percentage of evaluated participants meeting the registry definition of improvement. A participant met that definition if the total CDAI score improved by at least 70 points from baseline or fell below 150. The description also identifies CDAI below 150 as remission and CDAI above 450 as severe disease.

A rate endpoint reduces each participant's outcome to whether the specified improvement criterion was met, then reports the proportion meeting it among those evaluated. This can make the result easier to interpret as a response frequency, but it does not show the size of each participant's change or the distribution of CDAI scores. Those details would require continuous-score summaries or other outcome data.

Clinical improvement is used as a clinically interpretable measure of change in disease activity. The endpoint's interpretation depends on the stated threshold and the assessment time: this result concerns Week 8, not the other scheduled assessments. The registry record lists remission and other clinical measures as secondary outcomes, but the primary endpoint remains the Week 8 improvement rate as defined above.

The efficacy population description says participants had to take at least one dose and provide postdosing efficacy data. Its further wording about exclusions is truncated, so the complete population definition and handling of missing endpoint data are not reported in the registry record.

7. Results Posted in the Registry

• OPC-6535 25 mg: 20.0% (2/10) versus 10.0% (1/10) on control; risk difference 10.0 percentage points (95% CI -21.0 to 41.0), risk ratio 2.00 (0.21–18.69); unadjusted two-proportion z-test p = 0.531.

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.

Mean Change From the Baseline in Inflammatory Bowel Disease Questionnaire (IBDQ) Score After 8 Weeks of Study Drug Administration

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • OPC-6535 25 mg: mean 11.60 versus 5.00 on control; difference 6.60 (95% CI -9.53 to 22.73), standardized effect d = 0.36; z-test p = 0.423.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OPC-6535 25 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists seven secondary outcomes, including clinical improvement and remission at earlier assessments, CDAI change, IBDQ score change, endoscopic severity, and C-reactive protein. These outcomes span symptoms or disease-activity measures, quality of life, endoscopic assessment, and a laboratory marker. They could offer complementary descriptions of the study data, but they are not interchangeable with the primary Week 8 clinical improvement endpoint.

The posted secondary result with arm-level numerical summaries is the change in IBDQ score at Week 8. The registry record does not report detailed numerical results for most of the other listed secondary measures. It also lists no reported analyses. As a result, the overall secondary-outcome pattern cannot be assessed comprehensively from the registry record, and absence of a posted result should not be read as evidence of no change or no difference.

The posted IBDQ comparison is unadjusted, and its confidence interval includes no difference. It does not provide clear corroboration of the primary contrast, but it also cannot rule out effects on quality of life. The secondary outcomes differ in what they measure and when they are assessed, so a single result cannot stand in for all of them. Their relationship to the primary outcome is best understood as additional, potentially complementary evidence rather than a replacement for the primary endpoint.

Unadjusted secondary findings carry less weight because several outcomes and time points create multiple opportunities for chance patterns. General statistical explanation: without a prespecified hierarchy or multiplicity adjustment, isolated results are more difficult to interpret as confirmatory. The registry record does not report a multiplicity strategy, so secondary results should be viewed cautiously and in context rather than selectively elevated.

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

• Clinical Improvement Rate After 2 and 4 Weeks of Study Drug Administration
• Remission Rate (Number of Patients Showing Remission/Number of Patients Evaluated x 100) After 2, 4, and 8 Weeks of Study Drug Administration
• Clinical Improvement Rate (50) by Change in Total CDAI Score (Number of Subjects for Each Change/Number of Subjects Evaluated x 100) After 2, 4, and 8 Weeks of Study Drug Administration
• Mean Change From Baseline in Total CDAI Score After 2, 4, and 8 Weeks of Study Drug Administration
• Mean Change From the Baseline in Inflammatory Bowel Disease Questionnaire (IBDQ) Score After 8 Weeks of Study Drug Administration
• Mean Change From the Baseline in Crohn's Disease Endoscopic Index of Severity (CDEIS) Score After 8 Weeks of Study Drug Administration
• Mean Change in C-reactive Protein (CRP) Level From the Baseline After 4 and 8 Weeks of Study Drug Administration

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each evaluated participant either met the clinical improvement definition or did not. A rate is the number meeting the definition divided by the number evaluated, expressed as a percentage. The registry gives the rates and 95% confidence intervals separately for each arm. General statistical interpretation: a rate estimates the frequency of the defined outcome in the population represented by the participants, while uncertainty reflects that a different sample could produce a different observed rate.

What does the risk difference express?

The risk difference compares the event proportions by subtracting the placebo proportion from the active-treatment proportion. The posted 25 mg versus placebo estimate is 0.1, corresponding to the difference in the two observed proportions. A value of zero represents no difference in the estimated proportions. Values above or below zero indicate the direction of the contrast according to the comparison's stated arm ordering. The estimate is unadjusted, so it does not account for covariates or other factors beyond the group comparison.

The comparison also lists a risk ratio of 2.0, with a confidence interval from 0.214 to 18.69, and an odds ratio of 2.25, with a confidence interval from 0.170 to 29.77. These are alternative ways to express the 25 mg versus placebo contrast. A risk ratio compares the two event probabilities as a ratio; an odds ratio compares the odds of the event. General statistical explanation: ratios are relative measures and can look large even when the underlying event counts are small, so they should be read alongside the absolute rates and the risk difference. Here, both ratio intervals are very wide, reflecting substantial uncertainty.

How should the p-value be read?

The unadjusted p-value for the posted risk-difference comparison is 0.531. In general, a p-value describes how unusual data at least as discrepant from a specified null model would be if that model were true, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. The registry record does not identify the exact test used for this comparison, so no particular test procedure should be inferred.

Confidence intervals and p-values are related summaries of uncertainty, but the interval is especially useful for seeing the range of effect estimates compatible with the data under the interval method. The interval for the risk difference includes zero and spans effects in both directions. Thus the result is not a precise estimate of the contrast. A non-significant p-value does not show that the groups are equivalent; equivalence requires a prespecified margin and a suitable analysis, neither of which is reported in the registry record.

Why are the estimates uncertain?

There were 10 participants in the 25 mg group, 9 in the 50 mg group, and 10 in placebo for the posted primary outcome. With event counts this small, a change in the status of a participant can materially affect an arm's rate. General statistical explanation: sparse binary data often yield wide confidence intervals, and ordinary approximations can be sensitive to the method used. The registry record does not report the confidence-interval method, so the calculations cannot be independently attributed to a particular interval procedure.

Randomization is intended to support a fair comparison by balancing prognostic factors on average, but small randomized groups can still differ by chance. No baseline characteristics or adjusted analysis are reported with the primary result. The posted comparison is unadjusted, and the record does not report whether adjustment was planned or conducted.

The analysis population is described as participants who took at least one dose and provided postdosing efficacy data. The full description is incomplete, and the record does not explain how missing observations were handled, whether all randomized participants were included, or whether exclusions occurred. Those details matter because a complete-case rate can differ from an estimate based on all randomized participants if outcomes are missing in a way related to group or response.

The study listed several additional endpoints and assessment times. When multiple outcomes or comparisons are examined, the chance of observing an apparently notable result by chance can increase. General statistical explanation: multiplicity procedures can control that issue, but the registry record does not report a multiplicity adjustment or a prespecified hierarchy for the outcomes. The posted unadjusted comparisons should therefore be interpreted as exploratory rather than treated as a family of confirmatory tests.

Finally, a statistical estimate is not a complete account of design quality or clinical relevance. The registry record does not report the original sample-size assumptions, exact randomization and masking procedures, or a full analysis plan. The posted numbers can describe the observed data and their uncertainty, but cannot fill those gaps.

11. Confidence Intervals and Precision

The 95% confidence intervals around the arm-specific clinical improvement rates are wide: 2.5 to 55.6 for OPC-6535 25 mg, 7.5 to 70.1 for OPC-6535 50 mg, and 0.3 to 44.5 for placebo. The corresponding observed rates are 20.0%, 33.3%, and 10.0%. These intervals indicate substantial uncertainty about the underlying response rates; they are not guarantees that the true rate lies within the interval.

For the posted 25 mg versus placebo comparison, the risk difference is 0.1 with a 95% confidence interval from -0.210 to 0.410. Because this interval includes zero and reaches in both directions, it does not precisely locate the contrast. The lower end is compatible with a lower rate under 25 mg, while the upper end is compatible with a higher rate. The data therefore leave considerable uncertainty about both direction and magnitude.

The ratio measures are also imprecise: the risk ratio is 2.0 with a 95% confidence interval from 0.214 to 18.69, and the odds ratio is 2.25 with a 95% confidence interval from 0.170 to 29.77. Their breadth reinforces that the relative contrast is not precisely estimated. The reported confidence intervals for the 50 mg and placebo rates are not a substitute for a direct 50 mg versus placebo comparison interval, which is not reported in the registry record.

General statistical explanation: confidence-interval width depends on the amount of information in the data and on the interval method. Small samples and few events generally provide less precision. The registry record does not report the method used to calculate these intervals, so interpretation should focus on their reported range rather than assume a specific procedure.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm for 80% power and participants per arm for 90% power, for the specified 25 mg versus placebo comparison. They are illustrations based on the observed effect, not the trial's original design assumptions. The planning calculation uses a two-sided significance level 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 record does not report the trial's own original sample-size justification or planning assumptions.

The 80% power column describes the planned chance of detecting the stated effect under the calculation assumptions if that effect were the true one; the 90% column uses a higher target chance of detection. Both are prospective planning concepts. They do not describe the chance that the trial's observed result is correct, and they are not observed power.

For planning at 100% of the observed effect, the figures are 199 participants per arm for 80% power and 266 participants per arm for 90% power. For planning at 75% of the observed effect, they are 330 and 441 participants per arm. For planning at 50% of the observed effect, they are 686 and 918 participants per arm. The pattern illustrates a general principle: smaller effects require more participants to detect with the same target power, all else equal.

These are planning illustrations, not a recommendation or a reconstruction of the study's original plan. They use an observed estimate from a small trial, so the assumed effect itself is uncertain. The calculations concern only the listed comparison and assumptions; they do not establish what sample size would be appropriate for other endpoints, contrasts, or analysis methods.

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 = 0.100; treatment proportion p₁ = 0.200; average p̄ = 0.150.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5050 = 0.9897.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5000 = 0.4208.
4. n = (0.9897 + 0.4208)² / (0.1000)² = 199.0, rounded up to 199 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 <- 0.1                          # control proportion
p1 <- 0.2                          # 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(317369)
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 = 199 (80% power), 266 (90% power)
 75% of observed effect: n per arm = 330 (80% power), 441 (90% power)
 50% of observed effect: n per arm = 686 (80% power), 918 (90% power)
power.prop.test: 199 
Simulated power at n = 199 per arm: 0.812 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and several secondary outcomes, including assessments at different study weeks. It does not report whether the statistical plan specified a testing hierarchy, adjusted significance levels, or another approach to account for multiplicity. The number and structure of the planned comparisons are therefore not fully available.

General statistical explanation: when many outcomes, time points, or treatment contrasts are tested, the chance of at least one apparently unusual result can rise even if no underlying effects exist. Multiplicity procedures can address this problem, but their interpretation depends on which tests were planned and how they were grouped. Without those details, the posted unadjusted results should not be treated as though they were protected against multiple testing.

The record reports a primary efficacy population based on taking at least one dose and providing postdosing efficacy data. The description continues into an exclusion related to GCP violations but is truncated. The complete eligibility and exclusion rules for the analysis are not reported in the registry record. It also does not report the number randomized in each group, participant disposition, reasons for missing assessments, or the handling of missing data.

These omissions limit assessment of whether the analysis followed an intention-to-treat principle, whether participants were excluded after randomization, and whether missing outcomes could have affected the observed rates. No imputation method, sensitivity analysis, or alternative analysis population is reported in the registry record. The absence of these details does not show that such methods were not used; it means their use cannot be established from the record.

The original sample-size justification, detailed analysis plan, and interim-analysis plan are also not reported in the registry record. Consequently, the posted p-value and intervals can be described as reported, but the broader prespecified decision framework cannot be reconstructed. This matters particularly when reading secondary findings and interpreting a terminated study with small endpoint groups.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anal fistula (11.1%), haematuria (11.1%), subileus (10.0%).

The registry lists serious adverse events affecting 1 of 10 participants in the OPC-6535 25 mg group, 2 of 9 in the 50 mg group, and 0 of 10 in the placebo group. It lists other adverse events affecting 9 of 10, 9 of 9, and 8 of 10 participants, respectively. No deaths are listed in any group. These counts describe the recorded groups and should be read with their small denominators in mind.

The serious-event terms listed include Anal fistula at 11.1%, Haematuria at 11.1%, and Subileus at 10.0%. The registry record does not provide enough context in these summary figures to infer severity patterns beyond the reported serious-event classification, timing, relatedness, or whether the listed terms occurred in unique participants. The figures are descriptive and do not establish a comparative safety effect.

General statistical explanation: rare events are difficult to compare reliably in small groups, and a zero count does not demonstrate that an event cannot occur. The record does not report an inferential safety analysis or additional context needed to interpret causality. These summaries should therefore be understood as event counts in this trial, not as a complete safety profile.

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

The primary result describes the proportion of evaluated participants meeting a specified CDAI-based improvement definition at Week 8. In the posted groups, the rates were 20.0% with OPC-6535 25 mg, 33.3% with OPC-6535 50 mg, and 10.0% with placebo. The direct unadjusted estimate available is for 25 mg versus placebo: a risk difference of 0.1, with a 95% confidence interval from -0.210 to 0.410. That interval is wide and includes no difference, so the contrast is not estimated precisely.

The result does not establish that the 25 mg group differs from placebo, nor does it establish equivalence. It also does not establish the comparative effect of 50 mg, because a direct estimate and interval for that contrast are not reported in the registry record. Observed percentages are not enough by themselves to conclude that one group differs from another, particularly with small group sizes.

The endpoint captures a threshold-defined improvement at a particular assessment time. It does not describe all aspects of Crohn's disease, the magnitude of change for every participant, or longer-term outcomes. The registry record lists additional outcomes, but detailed results are not posted for most of them. The study summary also describes background 5-ASA and enteral-nutrition regimens, but does not report how those regimens were distributed by treatment group.

These data should be interpreted as an uncertain estimate from a phase 2 trial with 29 enrolled participants and a terminated status. The reason for termination, complete analysis-population details, missing-data handling, and original design assumptions are not reported in the registry record. The posted figures cannot answer questions beyond the population, endpoint, time point, and comparison they describe, and they are not a basis for medical advice.

17. Why This Trial Matters Statistically

This trial is statistically instructive because it pairs a simple, interpretable binary endpoint with very small group sizes. The event counts make clear why percentages alone can be misleading: the same rate can represent only a few participants, and the resulting uncertainty is substantial. Reading the arm-specific rates alongside the direct risk-difference interval gives a more complete picture than focusing on the point estimates.

The comparison also illustrates the distinction between the observed direction of an estimate and the precision of that estimate. The 25 mg point estimate is above the placebo rate, but its interval spans differences in both directions. A point estimate is not a settled conclusion, and a p-value is not a measure of effect size or certainty. The posted result remains compatible with materially different underlying contrasts.

The registry has three treatment groups, but the reported direct comparative analysis is only for 25 mg versus placebo. A numerical rate in the 50 mg group does not substitute for its own contrast and uncertainty interval. This distinction is important whenever multiple arms are present: descriptive group summaries and inferential comparisons answer different questions.

The record also illustrates how registry reporting affects interpretation. The status is terminated, but the reason is not reported; the efficacy-population description is incomplete; and the original sample-size and analysis plans are not reported. These missing details do not erase the posted data, but they constrain conclusions about participant flow, prespecification, and the intended inferential framework. Separating what the results estimate from what the record does not establish is central to responsible statistical reading.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The small endpoint groups—10 participants for 25 mg, 9 for 50 mg, and 10 for placebo—limit precision. The primary rate intervals are broad, and the 25 mg versus placebo risk-difference interval includes effects in both directions. The observed rates therefore should not be treated as stable estimates of the underlying response probabilities.

The record identifies the study as terminated but does not report the reason or the consequences for recruitment, follow-up, or analysis. It lists 29 participants enrolled, but does not provide a full participant-flow account or the number randomized by group. The efficacy-population description is truncated after mentioning GCP violations, and missing-data handling is not reported. These gaps limit evaluation of exclusions and potential missing-outcome bias.

Only a direct primary comparison of 25 mg versus placebo is posted. A comparative estimate for 50 mg versus placebo is not reported in the registry record, which prevents assessment of that contrast's uncertainty. The study summary describes different possible background regimens involving 5-ASA and enteral nutrition, but does not clarify their distribution across arms, limiting interpretation of the treatment context.

The record does not report the original sample-size justification, the detailed statistical plan, interim analyses, or a multiplicity approach. Most listed secondary outcomes do not have detailed numerical results in the registry record. The results are therefore limited both by the small study and by incomplete reporting of design and analysis details. These limitations are specific to what is documented and should not be mistaken for proof that unreported procedures were not performed.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Dose-finding Study of OPC-6535 in Patients With Active Crohn's Disease — NCT00317369.
• Registry record last updated 2021-02-15; status last verified 2021-01.
• Results first posted 2021-02-15.
• 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

NCT00317369 is a phase 2, randomized, double-masked, parallel-group study titled “A Dose-finding Study of OPC-6535 in Patients With Active Crohn's Disease.” The registry lists 29 participants enrolled, a start date of 2006-05, primary completion on 2007-07-11, and status as terminated.

The primary endpoint was the Week 8 clinical improvement rate, defined using change in total CDAI score. Rates were 20.0% for OPC-6535 25 mg, 33.3% for 50 mg, and 10.0% for placebo. The posted unadjusted 25 mg versus placebo risk difference was 0.1, with a 95% confidence interval from -0.210 to 0.410 and p = 0.531. The result is imprecise, and a comparative estimate for 50 mg is not reported in the registry record.

The record lists secondary outcomes and adverse-event summaries, but important details—including the reason for termination, full analysis-population description, missing-data methods, original sample-size justification, and detailed statistical plan—are not reported in the registry record.