A Dose-finding and Confirmatory Trial 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 and Confirmatory Trial of OPC-6535 in Patients With Active Crohn's Disease (NCT00989573), a randomized phase 2, phase 3 study. The primary outcome is Clinical Improvement Rate (Number of Subjects Showing Clinical Improvement / Number of Subjects Evaluated × 100) After 8 Weeks of IMP Administration.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, placebo-controlled trial recorded as Phase 2 and Phase 3. The official title describes it as multinational, multicenter, double-blind, and dose-finding and confirmatory. The registry lists quadruple masking. These labels describe the recorded design; the registry record does not explain which parties were masked or how masking was maintained. Allocation was randomized, but the method used to generate or conceal the allocation sequence is not reported in the registry record.

The three groups received once-daily oral placebo, OPC-6535 25 mg, or OPC-6535 50 mg for 8 weeks, alongside background treatment. The study summary specifies fixed oral 5-aminosalicylic acid, either alone or together with enteral nutrition. The record does not report how participants were assigned to those background-treatment options, whether use was balanced among groups, or whether it was considered in the primary analysis.

Recorded enrollment was 191. The brief summary describes the study purpose in 180 patients, but the record does not explain the relationship between that figure and recorded enrollment. Primary endpoint denominators in the full analysis set were 64 for OPC-6535 25 mg, 62 for OPC-6535 50 mg, and 61 for placebo. These analysis denominators differ from some safety denominators, which are reported separately.

The trial started in 2009-10, had primary completion in 2012-08, and is listed as completed. The sponsor was Otsuka Pharmaceutical Co., Ltd. The record does not report the planned allocation ratio, trial-specific sample-size justification, stopping rules, or whether interim analyses were conducted.

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: Full analysis set comprised all subjects who received at least one dose of IMP and for whom postdosing efficacy data were obtained.

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.

Population: Full analysis set comprised all subjects who received at least one dose of investigational medicinal product (IMP) and for whom postdosing efficacy data were obtained.

6. Primary Endpoint

The registry lists the primary outcome as Clinical Improvement Rate (Number of Subjects Showing Clinical Improvement / Number of Subjects Evaluated × 100) After 8 Weeks of IMP Administration, measured over Week 8.

The primary endpoint was the clinical improvement rate after 8 weeks, expressed as the percentage of participants meeting the registry's improvement definition. A participant counted as improved if the total Crohn's Disease Activity Index score decreased by at least 70 points from baseline or reached a value below 150. The description identifies a score below 150 as remission and a score above 450 as severe disease; those cutoffs help contextualize the scale but do not change the stated improvement rule.

A binary endpoint turns each participant's outcome into whether the improvement criterion was met or not met. The group rate is therefore the proportion of evaluated participants who met that criterion. The registry specifies a 95% confidence interval for each rate, which communicates uncertainty around the estimated percentage.

Clinical improvement is used as a study outcome because it applies a defined change in disease activity to each participant and permits a comparison of the proportions meeting the criterion in the randomized groups. It is not the same measure as remission alone: the improvement definition also allows a decrease of at least 70 points from baseline. The record lists remission and C-reactive protein outcomes among secondary measures, but their numerical results are not reported in the registry record.

The primary population was the full analysis set, defined as participants who received at least one dose of investigational medicinal product and had postdosing efficacy data. This definition makes clear that the primary rates do not necessarily use every randomized participant. The record does not report additional details of how missing endpoint data were handled.

7. Results Posted in the Registry

• OPC-6535 25 mg: 31.2% (20/64) versus 29.5% (18/61) on control; risk difference 1.7 percentage points (95% CI -14.4 to 17.9), risk ratio 1.06 (0.62–1.80); unadjusted two-proportion z-test p = 0.832.
• OPC-6535 50 mg: 21.0% (13/62) versus 29.5% (18/61) on control; risk difference -8.5 percentage points (95% CI -23.8 to 6.7), risk ratio 0.71 (0.38–1.32); unadjusted two-proportion z-test p = 0.275.

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.

Clinical Improvement Rate After 4 Weeks of IMP Administration

• 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:
  • OPC-6535 25 mg: 30.2% (19/63) versus 28.3% (17/60) on control; risk difference 1.8 percentage points (95% CI -14.3 to 17.9), risk ratio 1.06 (0.61–1.85); unadjusted two-proportion z-test p = 0.824.
  • OPC-6535 50 mg: 16.1% (10/62) versus 28.3% (17/60) on control; risk difference -12.2 percentage points (95% CI -26.8 to 2.4), risk ratio 0.57 (0.28–1.14); unadjusted two-proportion z-test p = 0.105.
• 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 95% confidence interval includes no difference, so these data do not show a statistically significant difference between OPC-6535 50 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering clinical improvement after 4 weeks, remission after 4 and 8 weeks, and mean change in C-reactive protein after 4 and 8 weeks. Numerical secondary results are posted for week-four clinical improvement. Remission and C-reactive protein results are not reported in the registry record, so the overall secondary-outcome picture is incomplete.

The week-four clinical improvement rates have a general pattern resembling the primary result: the 25 mg group and placebo have fairly similar observed rates, while the 50 mg group has a lower observed rate. The posted comparisons remain uncertain, and the week-four figures do not replace the prespecified primary endpoint at week 8. Considering an earlier time point can offer context about timing, but it does not independently resolve the uncertainty in the primary comparison.

Secondary outcomes can help describe whether the primary pattern is accompanied by other measures, but many outcomes create multiple opportunities to observe apparently notable results. If many tests are performed, the chance of at least one striking result under a no-effect model can increase. Adjustments or a hierarchy of outcomes can address this concern, but the multiplicity plan is not reported in the registry record. The week-four comparison p-values are unadjusted, and the record reports no formal analyses for the other listed secondary measures. These results therefore carry less evidential weight than a prespecified primary analysis and should be treated as supportive, exploratory descriptions rather than a separate confirmatory conclusion.

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

• Clinical Improvement Rate After 4 Weeks of IMP Administration
• Remission Rate (Number of Subjects Showing Remission / Number of Subjects Evaluated x 100) After 4 and 8 Weeks of IMP Administration
• Mean Change From Baseline in C-reactive Protein (CRP) Level After 4 and 8 Weeks of IMP Administration

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a percentage endpoint with a 95% confidence interval and posts dose-versus-placebo comparisons as risk differences. Together, these quantities address distinct questions: the rates describe outcomes within each group, while a risk difference describes the contrast between groups. The registry also posts unadjusted p-values and other effect measures, but it does not provide a full statistical analysis plan or the methods used to obtain every reported estimate.

What does a binary rate represent?

For a binary outcome, each participant either meets the endpoint definition or does not. The observed rate is the number meeting the definition divided by the number evaluated, expressed as a percentage. In this trial, the event is clinical improvement according to the stated Crohn's Disease Activity Index rule. The denominators are the full analysis set sizes reported for each group, not automatically the recorded enrollment total.

Rates are useful for describing what happened in each group, but a rate alone does not quantify the randomized contrast. The risk difference subtracts the placebo event probability from the event probability in the active-treatment group. A positive estimate means the observed event rate is higher in the active group; a negative estimate means it is lower. A value near zero indicates little observed separation. The confidence interval around that difference expresses uncertainty in the contrast, not uncertainty about whether individual participants improved.

How should the confidence intervals be understood?

A confidence interval is an interval estimate built from the observed data using a statistical procedure. In general, a 95% confidence interval describes the range of effect estimates reasonably compatible with the data and the procedure's assumptions. It is not a range containing 95% of individual participant outcomes, and it is not a statement that there is a 95% probability that the true effect lies inside this particular interval.

For the risk difference, zero represents no difference between the groups. When the interval includes zero, the data do not rule out no difference at the corresponding conventional confidence level. An interval can also include meaningful differences in both directions, which is a sign that the estimate is imprecise. The interval's width depends on the amount and pattern of information in the data and on the estimation method.

What does the p-value add?

A p-value is calculated under a specified null model, commonly a model in which the groups have no difference. It describes how unusual the observed data, or data more extreme, would be if that null model and the test assumptions held. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of an estimate. The posted values are unadjusted; the registry record does not report whether or how any adjustment for multiple comparisons was planned.

The comparison estimates are labelled as risk differences, and the record also includes risk ratios and odds ratios. These are alternative ways to express a binary-outcome contrast. A risk ratio compares the probabilities, while an odds ratio compares the odds. Different scales can make a contrast look different numerically, so the scale and its interpretation should be kept explicit. The reported confidence intervals for these measures are not interchangeable. The primary interpretation above emphasizes the risk difference because that is the stated comparison metric.

What is the analysis population?

The primary endpoint population is defined as the full analysis set: those who received at least one dose and had postdosing efficacy data. This is the registry's stated population definition. It does not establish that every randomized participant contributed an endpoint, and it is not equivalent to a documented intention-to-treat analysis unless the analysis plan defines it that way. The registry record does not report the number excluded from this population or the reasons for any exclusions.

Missing outcomes can affect estimates if participants without observed outcomes differ from those with observed outcomes. Common approaches include assumptions that missingness is unrelated to the outcome after accounting for observed information, or sensitivity analyses that examine alternative assumptions. These are general statistical considerations; the registry does not state which missing-data method, if any, was used for the primary outcome.

Why does over-dispersion matter?

Over-dispersion is a general concern in models for counts or clustered observations when the observed variation is larger than the model's assumptions allow. It can make standard errors too small if ignored. The primary endpoint is a binary percentage, and the posted record does not identify a count-model analysis or report an over-dispersion assessment. It would therefore be inappropriate to claim that over-dispersion was present or that a particular correction was used.

More generally, all inferential methods rely on assumptions about sampling, outcome measurement, and the analysis procedure. Randomization supports a fair comparison on average, but it does not by itself establish how missing data, protocol deviations, or multiple outcomes were handled. Details of those procedures are not reported in the registry record, so the posted summaries cannot answer every methodological question.

11. Confidence Intervals and Precision

The precision of an estimate is reflected in the width of its confidence interval. At week 8, the 25 mg versus placebo risk difference was 0.017, with a 95% confidence interval from -0.144 to 0.179. The 50 mg versus placebo risk difference was -0.085, with a 95% confidence interval from -0.238 to 0.068. Both intervals span zero and include effects in either direction. This means the observed estimates alone do not sharply distinguish a positive difference from no difference or a negative difference.

The confidence intervals for the separate group rates were 20.2% to 44.1% for OPC-6535 25 mg, 11.7% to 33.2% for OPC-6535 50 mg, and 18.5% to 42.6% for placebo. These intervals show uncertainty around each group's rate. They are not substitutes for the confidence interval of a between-group difference, because uncertainty in a contrast depends on both groups and the method used to estimate it.

Precision should not be confused with direction or importance. A narrow interval would indicate a more tightly estimated quantity, while a broad interval leaves a wider range of possible values compatible with the data. Whether a particular range is important in practice requires context and a prespecified threshold; such a threshold is not reported in the registry record. The reported intervals also do not address uncertainty from unreported analysis choices or missing-data assumptions.

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 illustrations based on the observed effect, not the trial's original design justification. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. For time-to-event outcomes, the convention would be total events; these outcomes are binary percentages, so the figures refer to participants per arm.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding per-arm planning amount for a 90% chance. These are prospective design calculations, not descriptions of what happened in the trial.

The rows use the observed effect, three-quarters of that effect, and half of that effect. Smaller effects require more participants to distinguish them from no difference with the same planned power and significance level. This is not observed power: it does not measure the probability that the completed trial detected an effect, and it should not be used to reinterpret the trial's results after the fact. The original sample-size assumptions and justification are not reported in the registry record.

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 = 0.295; treatment proportion p₁ = 0.312; average p̄ = 0.304.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6504 = 1.2747.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6503 = 0.5473.
4. n = (1.2747 + 0.5473)² / (0.0174)² = 10,942.3, rounded up to 10,943 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 <- 0.295081967213115                          # control proportion
p1 <- 0.3125                          # 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(989573)
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 = 10,943 (80% power), 14,649 (90% power)
 75% of observed effect: n per arm = 19,375 (80% power), 25,937 (90% power)
 50% of observed effect: n per arm = 43,416 (80% power), 58,120 (90% power)
power.prop.test: 10942.3 
Simulated power at n = 10,943 per arm: 0.797 (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 record lists one primary endpoint and several secondary outcome measures, including outcomes at more than one follow-up time. Multiple testing raises a general statistical concern: when many hypotheses are examined, some results may appear unusual by chance even when there is no underlying effect. Common strategies include identifying one primary comparison, controlling an overall error rate, specifying a testing hierarchy, or labeling secondary analyses exploratory. The registry record does not report a multiplicity procedure or how the primary and secondary tests were ordered.

The posted p-values for the dose-versus-placebo comparisons are unadjusted. They should be read as individual comparison results, not as values corrected for the number of doses, outcomes, or time points examined. The registry record reports no formal analyses for the other listed secondary outcomes. Without the analysis plan, it is not possible to determine whether additional tests were conducted or how their results were handled.

The full analysis set includes participants who received at least one dose and had postdosing efficacy data. The registry record does not report the number randomized but excluded from that set, the reasons for exclusion, or whether participants were analyzed according to their assigned group in all cases. It also does not report the handling of missing primary endpoint data, protocol deviations, or sensitivity analyses. Those details matter because missing outcomes and exclusions can affect how well the analyzed participants represent the randomized groups.

These are limitations of the information in the registry record, not proof that the trial lacked an appropriate analysis plan. The record does not provide enough detail to assess the original multiplicity strategy, missing-data assumptions, or analysis-population procedures. Interpretation should therefore stay close to the posted estimates and their stated uncertainty.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: crohn's disease (9.2%), abdominal mass (1.6%), diarrhoea (1.6%), intestinal obstruction (1.6%), pyrexia (1.6%).

Safety figures are reported for 65 participants in the OPC-6535 25 mg group, 63 in the 50 mg group, and 63 in the placebo group. Serious adverse events affected 8, 10, and 4 participants, respectively. Other adverse events affected 39, 35, and 33 participants, respectively. The record reports zero deaths in each group.

These are counts of participants affected, not counts of all event episodes. A participant may experience more than one event, so affected-participant totals should not be read as totals of distinct event occurrences. The registry also lists serious-event terms with percentages, including Crohn's disease at 9.2%, and abdominal mass, diarrhoea, intestinal obstruction, pyrexia, and intestinal abscess at 1.6% each. The record does not give arm-specific counts for those listed terms in the information available.

Safety counts are descriptive. Differences in counts do not by themselves establish that a treatment caused an event or that groups differ reliably in risk. The registry record does not provide detailed event narratives, exposure-adjusted rates, or a statistical comparison of safety outcomes.

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

The primary result describes the proportion of participants in each analysis group who met the registry's clinical improvement criterion after 8 weeks. The observed rates were 31.3% for OPC-6535 25 mg, 21.0% for OPC-6535 50 mg, and 29.5% for placebo. The corresponding dose-versus-placebo risk-difference intervals include zero and extend in both directions, so the estimates remain uncertain about the direction and size of any difference.

This does not establish that the groups were identical. A confidence interval that includes zero can be compatible with no difference and with nonzero differences. Nor does a numerical difference between observed rates, by itself, establish a dependable treatment effect. The registry record does not report a threshold for a clinically important difference, so the results cannot be judged against such a threshold from this record alone.

The endpoint is a defined measure of clinical improvement, not a complete account of every aspect of Crohn's disease or of longer-term outcomes. The study evaluated an 8-week treatment period. The registry lists remission and C-reactive protein as secondary outcomes, but numerical results for these measures are not reported in the registry record. The available endpoint therefore cannot answer questions about those outcomes or effects beyond the recorded follow-up.

Safety information is also limited to the posted counts and event terms. The counts describe affected participants and deaths, but they do not determine causation or provide a complete clinical assessment of safety. Further, the record does not report the full statistical plan, multiplicity handling, detailed missing-data procedures, or the original sample-size justification. The most defensible reading is a description of the observed trial results with substantial uncertainty, not a broader conclusion about treatment or individual care.

17. Why This Trial Matters Statistically

This trial is statistically instructive because its primary outcome is a binary rate, while the key scientific question concerns a contrast between randomized groups. Reporting both group rates and risk differences helps separate what was observed within each group from how much the groups differed. Confidence intervals make clear that an estimate's direction and precision matter alongside its point value.

The two dose comparisons illustrate why numerical ordering alone is not enough. The observed rate for the 25 mg group is close to placebo, whereas the 50 mg group has a lower observed rate. Yet both direct comparison intervals include zero and allow values in either direction. A point estimate is only one estimate from the trial data; the interval communicates how uncertain that estimate is.

The record also demonstrates the distinction between a trial's recorded enrollment, the study summary's planned purpose, and the analysis denominators. These numbers refer to different stages or populations, and should not be treated as interchangeable. Clear population definitions are essential when interpreting rates and their uncertainty.

Finally, the registry provides some statistical information but leaves important methods unreported. The planning illustrations are explicitly based on observed effects and are not the original design justification or a measure of observed power. Multiplicity procedures and missing-data handling are also not described. Keeping those boundaries visible helps prevent statistical summaries from being read as more definitive than the record supports.

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.

Several limitations are specific to the information recorded for this trial. The primary outcome is available as a short-term clinical improvement rate at week 8, but the record does not provide numerical results for the listed remission and C-reactive protein outcomes. The available outcome profile is therefore incomplete, and cannot establish whether those measures showed a similar or different pattern.

The primary analysis uses a full analysis set defined by treatment received and availability of postdosing efficacy data. The record does not report the number of randomized participants omitted from that population, reasons for omission, or how missing endpoint values were handled. That makes it difficult to assess the effect of exclusions or missingness on the estimates.

There is a difference between the recorded enrollment of 191 and the brief summary's description of a study purpose involving 180 patients. The registry record does not explain this relationship. The record also does not explain allocation-sequence generation or concealment, masking procedures, or management of the two base-treatment options.

Finally, the original sample-size calculation, multiplicity strategy, interim-analysis plan, and detailed analysis plan are not reported in the registry record. Those omissions limit evaluation of how the posted analyses relate to the original design. These caveats describe the available record; they do not establish that the trial did not have protocols or procedures addressing these issues.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Dose-finding and Confirmatory Trial of OPC-6535 in Patients With Active Crohn's Disease — NCT00989573.
• Registry record last updated 2021-04-06; status last verified 2021-03.
• Results first posted 2021-04-06.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The completed randomized, parallel-group trial evaluated once-daily oral OPC-6535 at 25 mg or 50 mg against placebo for 8 weeks in patients with active Crohn's disease, alongside specified base treatment. The registry lists Phase 2 and Phase 3 and describes multinational, multicenter, double-blind, placebo-controlled conduct, with quadruple masking recorded.

The primary endpoint was clinical improvement at week 8 in a full analysis set. Observed rates were 31.3% with 25 mg, 21.0% with 50 mg, and 29.5% with placebo. Both posted dose-versus-placebo risk-difference confidence intervals include zero. The record also reports week-four clinical improvement and safety counts; numerical remission and C-reactive protein results are not reported in the registry record.

Recorded enrollment was 191. The trial started in 2009-10 and reached primary completion in 2012-08. The posted summaries support a cautious description of the observed rates, uncertainty, and safety counts; important details of the original design assumptions and analysis procedures are not reported.