A Study to Assess the Efficacy and Safety of Risankizumab in Participants With Moderately to Severely Active Crohn's Disease Who Failed Prior Biologic Treatment: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Assess the Efficacy and Safety of Risankizumab in Participants With Moderately to Severely Active Crohn's Disease Who Failed Prior Biologic Treatment (NCT03104413), a randomized phase 3 study. The primary outcome is US Specific: Percentage of Participants With Crohn's Disease Activity Index (CDAI) Clinical Remission.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, double-blind, parallel-group, placebo-controlled induction study. The registry record lists Crohn’s disease as the condition, AbbVie as the sponsor, and the study status as completed. It records enrollment of 618 participants. The recorded start date is 2017-12-18, and the primary completion date is 2020-11-30.

During Induction Period 1, participants were assigned to placebo, risankizumab 600mg, or risankizumab 1200mg. For the primary endpoint, the registry reports analysis-group sizes of 187 for placebo and 191 for each risankizumab dose. These endpoint analysis counts are the relevant denominators for interpreting the posted Week 12 percentages; they should not be treated as a count of everyone enrolled.

The registry also describes Induction Period 2 groups, including participants who received placebo in Period 1 and some participants with inadequate response at Week 12 who were randomized to further risankizumab treatment. Those later-period groups do not constitute the randomized placebo comparison used for the primary Week 12 result. The posted safety record includes Period 2 groups as well as Period 1 groups, so the period and group labels matter when reading those figures.

The registry record does not report the original sample-size justification, the full allocation procedure, or the detailed operational procedures used to maintain masking. It describes the study as randomized and double-blind, but further details about implementation are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: A total of 618 subjects were enrolled and 605 were included in the intent-to-treat (ITT) population; 569 of those had a baseline eligible Simple Endoscopic Score for Crohn's disease (SES-CD) of ≥ 6 (≥ 4 for isolated ileal disease) excluding the narrowing component and were included in the ITT1A population. This population was the primary population for both the United States (US) specific as well as the Global (Outside the US) efficacy analysis' of the 12-Week Induction Period.

Only the first 6 of 7 groups are shown.

Induction Period 1

Induction Period 2

Analysis population for the primary outcome, as defined in the registry: Intent to Treat 1A Population: all randomized subjects who received at least one dose of study drug during Induction Period 1 and had baseline eligible SES-CD of ≥ 6 (≥ 4 for isolated ileal disease) excluding the narrowing component.

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: The safety population (SA) consists of all subjects who received at least 1 dose of study medication.

6. Primary Endpoint

The registry lists the primary outcome as US Specific: Percentage of Participants With Crohn's Disease Activity Index (CDAI) Clinical Remission, measured over Week 12.

The primary endpoint is the percentage of participants with Crohn’s Disease Activity Index (CDAI) clinical remission at Week 12. The registry defines remission as CDAI < 150. The CDAI combines information from 8 components: 7 are based on participant diary entries, interviews, physical examinations, and body-weight and height measurements, while 1 is based on laboratory analysis.

A remission endpoint turns a multi-component disease activity measure into a clinically interpretable binary outcome: each participant either meets the stated threshold or does not. Reporting the percentage meeting that definition allows comparison of the proportion reaching the endpoint in each randomized group. It does not show the full range of CDAI values or the degree of change for participants who do not meet the threshold.

The endpoint is restricted to the registry’s Intent to Treat 1A Population. This includes randomized participants who received at least one study-drug dose during Induction Period 1 and met the specified baseline endoscopic eligibility requirement, with the narrowing component excluded. That population definition is important: the primary percentages are not described as estimates for every person enrolled regardless of eligibility or treatment exposure.

Clinical remission is one way to summarize disease status at a specified assessment time. The Week 12 endpoint does not, on its own, describe how long remission lasts, how symptoms changed at other times, or what happened after the induction assessment.

7. Results Posted in the Registry

• Risankizumab 600mg (Induction Period 1): 41.9% (80/191) versus 19.8% (37/187) on control; risk difference 22.1 percentage points (95% CI 13.1 to 31.1), risk ratio 2.12 (1.52–2.95); unadjusted two-proportion z-test p = <0.001.
• Risankizumab 1200mg (Induction Period 1): 40.3% (77/191) versus 19.8% (37/187) on control; risk difference 20.5 percentage points (95% CI 11.5 to 29.5), risk ratio 2.04 (1.46–2.85); unadjusted two-proportion z-test p = <0.001.

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.

US Specific: Percentage of Participants With Clinical Remission

• 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:
  • Risankizumab 600mg (Induction Period 1): 34.6% (66/191) versus 19.3% (36/187) on control; risk difference 15.3 percentage points (95% CI 6.5 to 24.1), risk ratio 1.79 (1.26–2.55); unadjusted two-proportion z-test p = <0.001.
  • Risankizumab 1200mg (Induction Period 1): 39.8% (76/191) versus 19.3% (36/187) on control; risk difference 20.5 percentage points (95% CI 11.6 to 29.5), risk ratio 2.07 (1.47–2.91); 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 Risankizumab 600mg (Induction Period 1) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Risankizumab 1200mg (Induction Period 1) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

US Specific: Percentage of Participants With Crohn's Disease Activity Index (CDAI) Clinical Response

• 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:
  • Risankizumab 600mg (Induction Period 1): 36.6% (70/191) versus 20.9% (39/187) on control; risk difference 15.8 percentage points (95% CI 6.8 to 24.8), risk ratio 1.76 (1.26–2.46); unadjusted two-proportion z-test p = <0.001.
  • Risankizumab 1200mg (Induction Period 1): 32.5% (62/191) versus 20.9% (39/187) on control; risk difference 11.6 percentage points (95% CI 2.8 to 20.4), risk ratio 1.56 (1.10–2.20); unadjusted two-proportion z-test p = 0.011.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Risankizumab 600mg (Induction Period 1) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Risankizumab 1200mg (Induction Period 1) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

US Specific: Change From Baseline of Functional Assessment of Chronic Illness Therapy (FACIT)-Fatigue

• 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 errors.
• Result:
  • Risankizumab 600mg (Induction Period 1): mean 10.50 versus 7.70 on control; difference 2.80 (95% CI 0.47 to 5.13), standardized effect d = 0.27; z-test p = 0.018.
  • Risankizumab 1200mg (Induction Period 1): mean 10.80 versus 7.70 on control; difference 3.10 (95% CI 0.77 to 5.43), standardized effect d = 0.29; z-test p = 0.009.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Risankizumab 600mg (Induction Period 1) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Risankizumab 1200mg (Induction Period 1) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover additional remission and response measures, symptom-related endpoints, and fatigue. The pattern across the reported results is broadly consistent with the primary endpoint: the posted comparisons generally show higher endpoint values for risankizumab groups than placebo in the listed induction-period comparisons. The endpoints measure different aspects of disease activity and participant experience, however, so they are supporting evidence rather than interchangeable versions of the primary outcome.

The registry includes secondary analyses at different assessment times and uses different outcome scales. Some are binary percentages, while FACIT-Fatigue is a change-from-baseline measure reported in scale units. The statistical interpretation should follow each endpoint’s own definition and analysis rather than treating every result as a common measure of remission. The registry’s secondary outcome list includes repeated outcome descriptions, and the record notes 31 posted secondary outcomes.

The secondary findings add context to the primary Week 12 result, but they should carry less inferential weight when the multiplicity strategy is not reported. In general, testing many outcomes can make isolated small p-values less persuasive unless the analysis plan defines how those tests are handled. The registry record does not report a complete adjustment or hierarchy for the secondary endpoints, so their p-values should be read as reported, without assuming a multiplicity correction.

These secondary outcomes do not establish the durability of the primary endpoint or a direct difference between the risankizumab doses. They also do not remove the need to consider the population definitions, assessment times, and analysis methods attached to each outcome.

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

• US Specific: Percentage of Participants With Clinical Remission
• US Specific: Percentage of Participants With Crohn's Disease Activity Index (CDAI) Clinical Response
• US Specific: Percentage of Participants With Crohn's Disease Activity Index (CDAI) Clinical Response
• US Specific: Change From Baseline of Functional Assessment of Chronic Illness Therapy (FACIT)-Fatigue
• US Specific: Percentage of Participants With Crohn's Disease Activity Index (CDAI) Clinical Remission
• US Specific: Percentage of Participants With CDAI Clinical Response and Endoscopic Response
• US Specific: Percentage of Participants With Stool Frequency (SF) Remission
• US Specific: Percentage of Participants With Abdominal Pain (AP) Remission

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary endpoint such as meeting or not meeting the CDAI remission definition, the outcome can be expressed as a percentage in each group. A risk difference expresses the contrast between two such percentages in percentage-point terms. The registry’s primary sponsor analyses report adjusted risk differences, while the simple recalculations use the posted group counts and percentages without adjustment. These approaches need not produce exactly the same estimate, because adjustment and the underlying analysis procedure can affect a comparison.

What does adjustment do?

In general, an adjusted analysis accounts for selected features of the data when estimating a group contrast. The registry identifies the sponsor’s method as Cochran-Mantel-Haenszel and labels the parameter as an adjusted risk difference. The particular stratification or adjustment details are not reported in the registry record, so the reported values should be read as the sponsor’s adjusted estimates rather than reconstructed from an assumed model.

The sponsor reports the primary comparisons as 22.1 for 600mg versus placebo and 20.5 for 1200mg versus placebo, with their respective 95% confidence intervals and p-values. The posted percentages and recalculated unadjusted comparisons are useful descriptive companions, but they do not replace the sponsor’s adjusted analysis. The record lists no discrepancy flag between the recalculation and sponsor results.

What does a confidence interval convey?

In general, a confidence interval describes the range of estimates compatible with the observed data under the method’s assumptions. It communicates precision as well as direction: a narrower interval indicates less statistical uncertainty than a wider interval on the same scale. It is not a range that guarantees the true value lies within its endpoints, and it does not account automatically for every possible source of bias or uncertainty.

For the primary sponsor analyses, the intervals are reported at 95% confidence. Each interval is above zero, consistent with the registry’s superiority labels and reported p-values for the respective placebo comparisons. This statement concerns the reported adjusted contrasts and does not establish a direct difference between the two risankizumab groups.

Why distinguish adjusted from unadjusted results?

The recalculated values use the posted summary statistics to make a simple comparison between two groups. They are not a reanalysis of participant-level data. The sponsor’s analysis may incorporate aspects of the trial analysis that are unavailable in summary results. Accordingly, the sponsor’s own analysis takes precedence if a discrepancy is flagged; no such discrepancy is flagged in this record. Even without a flagged discrepancy, the two types of result should be identified accurately rather than presented as interchangeable.

The registry also reports secondary outcomes with different forms. Binary outcomes are expressed as percentages, while FACIT-Fatigue is reported as change from baseline in units on a scale, with least-squares means and standard errors. In general, continuous outcomes retain more information about the range of measured values than a binary threshold does. The sponsor’s FACIT-Fatigue analysis is identified as a Mixed-Effect Model Repeat Measurement, whereas the simple recalculation from summaries is only an approximation and does not reproduce that model.

What do the planning illustrations mean?

In general, a power calculation asks how many participants a planned comparison might require under stated assumptions to have a specified chance of detecting an effect of a chosen size at a chosen significance level. The planning illustrations use the observed effect or a stated fraction of it. They are not a retrospective measure of the trial’s success and do not establish that the original study was designed using those assumptions. The registry record does not report the original design calculation or its assumptions.

For a binary outcome, the variability depends on the event proportions as well as group size. In other statistical settings, over-dispersion means that observed variability exceeds what a simpler model assumes; accounting for it can widen uncertainty or change required sample sizes. That general issue should not be attributed to this trial’s primary analysis without a reported method or evidence that over-dispersion was modeled.

Finally, multiple endpoints and comparisons create a multiplicity question: when many hypotheses are tested, the chance of at least one apparently notable result can increase if no adjustment or prespecified hierarchy is used. The registry record does not report a complete multiplicity procedure, so the secondary p-values should not be treated as if a particular correction had been applied.

11. Confidence Intervals and Precision

The primary group percentages are accompanied by 95% confidence intervals. For placebo, the interval is 14.1 to 25.5; for risankizumab 600mg, it is 34.9 to 49.0; and for risankizumab 1200mg, it is 33.4 to 47.3. These intervals show uncertainty around the estimated remission percentage in each group. They do not describe the spread of individual participants’ outcomes.

The sponsor’s adjusted risk-difference interval is 13.1 to 31.0 for 600mg versus placebo and 11.6 to 29.5 for 1200mg versus placebo. Both intervals are on the positive side of zero and are consistent with the corresponding reported p-values. The width of an interval matters: it indicates that the data are compatible with a range of effect sizes, not only the point estimate. A point estimate should therefore be read together with its interval rather than as an exact effect.

The intervals for the two comparisons share a range of values. That overlap does not itself test whether the doses differ, and the registry does not report a direct dose-versus-dose analysis for this endpoint. Nor do these confidence intervals account for uncertainty arising from unreported analytic choices, missing-data handling, or the broader set of outcomes.

In general, confidence intervals quantify sampling uncertainty under the method used. They do not correct for possible selection, measurement, or reporting bias. Precision should therefore be considered alongside the randomized design, the defined analysis population, and the limits of what the registry record documents.

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 illustrations are expressed as participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. For each comparison, the figures are based on planning for the observed effect, 75% of the observed effect, or 50% of the observed effect. For example, the primary 600mg comparison lists 68 participants per arm for 80% power and 90 participants per arm for 90% power when planning for 100% of the observed effect. When planning for 75% of that effect, the corresponding figures are 115 and 153; for 50%, they are 242 and 324.

In plain terms, the 80% power column describes a planning scenario with an 80% chance of detecting the stated effect if the assumptions hold and that effect is real. The 90% power column uses a higher target chance under those same types of assumptions. These are planning probabilities, not the chance that a result is true. Smaller effects require more participants in the illustrated calculations: the entries for 50% of the observed effect are larger than those for the full observed effect.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The figures are planning illustrations computed from the observed effect, not the trial’s original design calculation. They are not observed power. The registry record does not report the original design assumptions or sample-size justification.

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 = 0.198; treatment proportion p₁ = 0.419; average p̄ = 0.308.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6531 = 1.2801.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6341 = 0.5337.
4. n = (1.2801 + 0.5337)² / (0.2210)² = 67.4, rounded up to 68 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 <- 0.197860962566845                          # control proportion
p1 <- 0.418848167539267                          # 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(3104413)
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 = 68 (80% power), 90 (90% power)
 75% of observed effect: n per arm = 115 (80% power), 153 (90% power)
 50% of observed effect: n per arm = 242 (80% power), 324 (90% power)
power.prop.test: 67.4 
Simulated power at n = 68 per arm: 0.810 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary analyses are adjusted comparisons using the Cochran-Mantel-Haenszel method. They report an adjusted risk difference of 22.1 for risankizumab 600mg versus placebo, with a 95% confidence interval of 13.1 to 31.0 and p < 0.001; and 20.5 for risankizumab 1200mg versus placebo, with a 95% confidence interval of 11.6 to 29.5 and p < 0.001.

The unadjusted recalculations are simple comparisons based on the posted group summaries, rather than reproductions of the sponsor’s analysis using participant-level data. The two approaches can differ because the sponsor’s analysis is adjusted. The record does not flag a discrepancy between the sponsor results and recalculations. Therefore, the sponsor’s reported analyses remain the primary inferential results, with the recalculations serving as descriptive cross-checks rather than replacements.

The record labels both sponsor comparisons as superiority. That label describes the reported analysis conclusion for each placebo comparison; it does not imply a reported superiority comparison between risankizumab doses. The details of all adjustment factors are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, time points, groups, or statistical contrasts. In general, the more hypotheses examined, the greater the chance that at least one result appears notable by chance if each is interpreted independently. Common approaches include prespecifying a hierarchy of tests or adjusting the significance criteria, but the appropriate approach depends on the trial’s protocol and analysis plan.

The registry lists 35 outcome measures and 70 analyses, and it records 31 posted secondary outcomes. The record gives sponsor-reported p-values for the primary endpoint and several secondary outcomes, but a complete strategy for controlling multiplicity is not reported in the registry record. Therefore, the reported secondary p-values should be read as individual results; it is not possible from this record to establish whether they were adjusted, tested in a prespecified order, or intended as confirmatory evidence.

The primary analysis population is described as the Intent to Treat 1A Population, with inclusion requiring randomization, receipt of at least one dose during Induction Period 1, and eligible baseline SES-CD. This is the stated population for the primary endpoint, not an unrestricted all-enrolled population. The registry does not report the full details of how missing primary endpoint values were handled, the amount of missing data by group, or the assumptions used for any imputation. Those details can affect interpretation of a binary endpoint.

The record also does not report the complete statistical analysis plan, interim analyses, or original sample-size justification. These omissions do not negate the posted results, but they limit independent assessment of prespecification, missing-data sensitivity, and the intended role of secondary analyses. The endpoint definitions and reported analysis population should therefore be kept in view when interpreting the stated estimates.

16. 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: crohn's disease (9.7%), abdominal pain (4.9%), nausea (2.4%), pyrexia (2.4%), intestinal obstruction (2.4%).

The registry reports serious adverse events and other adverse events by group, alongside numbers at risk and deaths. In Induction Period 1, the serious adverse event figures are 26 among 207 for placebo, 10 among 206 for risankizumab 600mg, and 9 among 205 for risankizumab 1200mg. The other adverse event figures are 51 among 207, 32 among 206, and 32 among 205, respectively. Deaths are recorded as 0, 0, and 2 for those groups.

The registry also reports Period 2 safety groups, including a Period 2 risankizumab total with 16 serious adverse events among 211, 28 other adverse events among 211, and 1 death. Period 2 groups reflect the later treatment period and should not be read as a continuation of the initial randomized placebo comparison without regard to their group definitions and treatment histories.

The listed serious adverse event terms include Crohn’s disease at 9.7%, abdominal pain at 4.9%, nausea at 2.4%, pyrexia at 2.4%, intestinal obstruction at 2.4%, and sepsis at 2.4%. The registry’s listed terms and event counts do not, by themselves, establish that treatment caused an event or provide a complete comparative safety analysis. These figures describe what was recorded in the registry, not individualized risk estimates.

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

The primary result describes the percentage meeting a specific CDAI remission threshold at Week 12 in the registry-defined analysis population. The posted percentages are higher in both risankizumab groups than in the placebo group, and the sponsor’s adjusted analyses report positive risk differences with 95% confidence intervals above zero. Those statements summarize the observed randomized comparisons during Induction Period 1.

The result does not mean that every participant in a risankizumab group met the remission definition. It does not predict an individual participant’s response, and it does not say how a participant who did not meet the threshold changed on the underlying CDAI measure. Nor does a Week 12 outcome establish how long remission might persist or what later outcomes would be.

The primary comparisons are each against placebo. They do not show that 600mg is superior or equivalent to 1200mg, because the registry does not report a direct dose-versus-dose primary analysis. A difference between the two group percentages is not itself evidence of a statistically supported dose difference.

The estimates are specific to participants meeting the Intent to Treat 1A eligibility and treatment-exposure definition. Generalization to people outside that described population, to other treatment settings, or to outcomes beyond the induction period is not established by these data alone. Interpretation also depends on the endpoint definition, missing-data handling, and statistical plan; some of those details are not reported in the registry record.

Finally, statistical evidence and clinical importance are not identical. A p-value addresses compatibility with a statistical null under specified assumptions; the effect estimate and interval show the estimated magnitude and its uncertainty. Decisions about the importance of an endpoint require context beyond a p-value, and no medical advice follows from these registry statistics alone.

18. Why This Trial Matters Statistically

This trial offers a randomized placebo comparison for a defined induction-period endpoint in participants with moderately to severely active Crohn’s disease who failed prior biologic treatment. Random allocation and double masking are important design features because, in general, they can reduce some sources of bias in treatment comparisons. The registry reports that design, while details of implementation are not reported.

Statistically, the result is useful because it includes both group-level remission percentages and sponsor-reported adjusted risk differences with confidence intervals. Looking at the absolute percentages helps make the outcome concrete; the risk differences describe the contrast between groups; and the intervals communicate uncertainty around the estimated contrasts. These are complementary ways to read the same primary endpoint, not separate pieces of proof.

The record also illustrates why analysis definitions matter. The primary endpoint is tied to a threshold on a multi-component index and to an explicitly defined analysis population. Results are most interpretable when that threshold, population, assessment time, and comparison are considered together. Separating sponsor-adjusted results from simple unadjusted recalculations also prevents summary-data calculations from being mistaken for the trial’s full analysis.

At the same time, the registry leaves important interpretive details unreported, including the original sample-size rationale, full missing-data handling, and multiplicity strategy. Those limits matter particularly when reading numerous secondary results. The strongest statistical reading therefore emphasizes the prespecified-looking primary comparison as reported, while treating unadjusted secondary findings and planning illustrations as contextual rather than definitive evidence.

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.

The registry record does not report the original sample-size justification or the assumptions used to plan the trial. Planning illustrations based on the observed effect cannot reveal what effect the study was originally designed to detect. The record also does not report the complete statistical analysis plan, full adjustment factors for the primary Cochran-Mantel-Haenszel analyses, or the strategy for handling multiplicity across outcomes.

Missing-data handling for the primary endpoint and secondary outcomes is not reported in enough detail to evaluate how absent assessments may have affected the estimates. The primary population requires receipt of at least one dose and baseline endoscopic eligibility, so it is important not to interpret the endpoint percentages as applying to every enrolled participant.

The study addresses an induction period, with the primary endpoint assessed at Week 12. The posted primary result therefore does not characterize longer-term outcomes. The registry’s Period 2 safety groups have different treatment histories and should not be treated as directly comparable randomized groups without further design and analysis details.

The registry reports multiple secondary outcomes and analyses, but the multiplicity approach is not reported. Accordingly, the secondary p-values do not have an established confirmatory interpretation from this record alone. The registry also does not supply participant-level data for independently reproducing the sponsor’s adjusted analyses. Simple recalculations from summary statistics can check broad patterns but cannot reproduce all features of those analyses.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Assess the Efficacy and Safety of Risankizumab in Participants With Moderately to Severely Active Crohn's Disease Who Failed Prior Biologic Treatment — NCT03104413.
• Registry record last updated 2022-06-14; status last verified 2021-08.
• Results first posted 2022-06-14.
• 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

The registry record describes NCT03104413, a completed Phase 3, randomized, double-blind, parallel, placebo-controlled induction study sponsored by AbbVie. It evaluated risankizumab against placebo in participants with moderately to severely active Crohn’s disease who failed prior biologic treatment. Enrollment is recorded as 618.

The primary endpoint was the percentage of participants meeting CDAI clinical remission at Week 12, defined as CDAI < 150, in the Intent to Treat 1A Population. The posted percentages were 19.8 for placebo, 42.0 for risankizumab 600mg, and 40.3 for risankizumab 1200mg. The sponsor reported adjusted risk differences of 22.1 and 20.5 against placebo, with 95% confidence intervals above zero and p-values reported as < 0.001.

Secondary outcomes and safety figures provide additional context, but multiplicity handling, detailed missing-data methods, and the original sample-size rationale are not reported in the registry record.