Efficacy and Safety of Two Treatment Algorithms in Adults With Moderate to Severe Crohn's Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Two Treatment Algorithms in Adults With Moderate to Severe Crohn's Disease (NCT01235689), a randomized phase 3 study. The primary outcome is Percentage of Participants With Mucosal Healing and No Deep Ulcerations.

2. Clinical Question

3. Trial Design

This was a randomized, open-label, multicenter, parallel-group Phase 3 study in adults with moderate to severe Crohn's disease. Participants were assigned to Tight Control Management or Clinically Driven Management. The registry records enrollment of 252 and lists the study as completed. The study start date was 2011-02-11, and the primary completion date was 2016-11-03.

The contrast was between management strategies rather than a comparison of a single fixed drug against another. Tight Control Management used CDAI, hs-CRP, fecal calprotectin, and corticosteroid use to guide disease-activity management. Clinically Driven Management used CDAI and corticosteroid use. In both arms, customized therapy could include prednisone, adalimumab, and azathioprine. The available arm descriptions are incomplete, so further details about treatment decisions, treatment sequences, or permitted changes are not reported in the registry record.

Because the study was open-label, participants and study personnel were not masked to management assignment. The primary endpoint included an endoscopic assessment at 48 weeks after randomization, with ileocolonoscopies evaluated by the site. The registry describes the primary analysis population as all randomized participants and specifies that missing CDEIS values from endoscopies performed at that time were counted as non-responders.

The registry record does not report the original sample-size justification, the detailed randomization procedure, or the full statistical analysis plan. It also does not report whether any interim analyses were planned or performed. Those design details should not be inferred from the posted outcome results or from the separate planning illustrations.

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 252 participants were enrolled and received study treatment, of whom * 165 entered the prednisone run-in * 157 randomized (45 prior to Week 9, 112 at Week 9) * 8 discontinued prior to randomization. * 87 randomized at Baseline. Randomization was stratified by smoking status, weight, and disease duration.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants; Participants with missing CDEIS values from endoscopies performed 48 weeks after randomization were imputed as non-responders.

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 Percentage of Participants With Mucosal Healing and No Deep Ulcerations, measured over 48 weeks after Randomization.

The primary endpoint was the percentage of participants with mucosal healing and no deep ulcerations at 48 weeks after randomization. Mucosal healing was defined as CDEIS < 4. The second part required absence of all deep ulcerations in all segments explored in CDEIS. CDEIS is an index of endoscopic Crohn's disease severity that considers deep and superficial ulcerations, ulcerated and non-ulcerated surface, and ulcerated or non-ulcerated stenosis across five predefined segments. Its score ranges from 0 to 44, with higher scores indicating more severe endoscopic activity.

The combined endpoint represents a specific endoscopic state: a participant had to meet the mucosal-healing threshold and also have no deep ulcerations. It is therefore more restrictive than a measure based on CDEIS alone. The registry says the ileocolonoscopies were evaluated by the site; central reading or blinded assessment is not reported in the registry record.

Endoscopic outcomes are used to assess disease activity in the intestinal lining rather than relying only on symptoms or clinical activity measures. That is a general explanation of the role of an endoscopic endpoint, not a claim about how participants felt or functioned. The primary endpoint does not by itself summarize every aspect of Crohn's disease or treatment experience. Missing CDEIS values at the specified assessment were counted as non-responders, so the posted percentage combines observed endpoint status with that prespecified missing-value classification.

7. Results Posted in the Registry

• Clinically Driven Management: 30.3% (37/122) versus 45.9% (56/122) on control; risk difference -15.6 percentage points (95% CI -27.6 to -3.5), risk ratio 0.66 (0.47–0.92); unadjusted two-proportion z-test p = 0.012.

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.

Percentage of Participants in Deep Remission 48 Weeks After Randomization

• 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:
  • Clinically Driven Management: 23.0% (28/122) versus 36.9% (45/122) on control; risk difference -13.9 percentage points (95% CI -25.3 to -2.6), risk ratio 0.62 (0.42–0.93); unadjusted two-proportion z-test p = 0.017.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Clinically Driven Management than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants in Biologic Remission 48 Weeks After Randomization

• 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:
  • Clinically Driven Management: 15.6% (19/122) versus 29.5% (36/122) on control; risk difference -13.9 percentage points (95% CI -24.3 to -3.6), risk ratio 0.53 (0.32–0.87); unadjusted two-proportion z-test p = 0.009.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Clinically Driven Management than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Mucosal Healing 48 Weeks After Randomization

• 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:
  • Clinically Driven Management: 30.3% (37/122) versus 45.9% (56/122) on control; risk difference -15.6 percentage points (95% CI -27.6 to -3.5), risk ratio 0.66 (0.47–0.92); unadjusted two-proportion z-test p = 0.012.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Clinically Driven Management than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover remission, mucosal healing, and other endoscopic or clinical activity measures. The results for the displayed measures of deep remission, biologic remission, and mucosal healing follow the same general direction as the primary endpoint: the reported percentages are higher under Tight Control Management than under Clinically Driven Management. This overall pattern is consistent with the primary finding at the level of the posted summaries, but it does not establish that every secondary outcome had the same pattern or the same degree of precision.

Secondary outcomes add context by examining related but distinct definitions of disease status. They should not be treated as repeated versions of the primary endpoint. For example, the primary endpoint requires mucosal healing together with no deep ulcerations, while other posted outcomes use their own definitions. The registry lists 33 outcome measures and 14 analyses, and 32 secondary outcome measures are posted. The available record does not describe how all those outcomes relate to a single testing strategy.

The registry does not report a multiplicity adjustment. When many outcomes are examined, the chance of obtaining at least one apparently notable result can increase, even if each individual test uses a conventional threshold. This is a general statistical concern, not evidence that any particular secondary finding is false. Because the posted secondary results are not described as adjusted for multiplicity, they carry less confirmatory weight than the primary comparison. Their p-values should be considered exploratory unless the registry record reports a more specific prespecified testing hierarchy, which it does not.

The secondary findings can support a coherent description of the posted outcome pattern, but they do not independently prove a broad treatment effect across all dimensions of Crohn's disease. The primary endpoint remains the main result for the study's stated objective. Interpretation of any additional outcome also depends on its definition, missing-data handling, and analysis population; where those details are absent, they are not reported in the registry record.

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

• Percentage of Participants in Deep Remission 48 Weeks After Randomization
• Percentage of Participants in Biologic Remission 48 Weeks After Randomization
• Percentage of Participants With Mucosal Healing 48 Weeks After Randomization
• Percentage of Participants With Mucosal Healing and CDEIS < 4 in Every Segment 48 Weeks After Randomization
• Percentage of Participants With Complete Mucosal Healing 48 Weeks After Randomization
• Percentage of Participants With Endoscopic Response 48 Weeks After Randomization
• Change From Baseline in CDEIS at 48 Weeks After Randomization
• Change From Baseline in CDAI Over Time

9. Statistical Interpretation

10. Statistical Methods Explained

The primary result combines a binary endpoint, a group comparison, and a rule for missing endoscopic assessments. Each part affects what the reported percentages and statistical tests mean. The explanations below are general descriptions of those methods, alongside the specific methods identified in the registry.

What does a percentage endpoint represent?

A binary endpoint classifies each participant as meeting or not meeting a defined condition. For this primary endpoint, meeting the condition required both mucosal healing, defined as CDEIS < 4, and no deep ulcerations in any segment explored in CDEIS. The posted group percentages describe the proportion classified as meeting that combined definition under the registry's analysis rules. They do not describe the average CDEIS score, and they do not show how far above or below the threshold individual participants were.

Binary outcomes are straightforward to explain, but they discard detail about the degree of change within either category. A participant just meeting the criterion and one with a more extensive endoscopic improvement are both counted as responders. Conversely, a participant who does not meet the full combined endpoint is counted as a non-responder even if some component of endoscopic status improved. That is a general property of threshold-based outcomes, not a separate result from this study.

What is a risk difference?

A risk difference subtracts the event proportion in one group from the event proportion in another. It is expressed on the absolute probability scale, and its sign depends on the order of subtraction. The re-calculated estimate is reported as Clinically Driven Management relative to Tight Control Management; its negative sign indicates a lower observed endpoint proportion in the first named group in this comparison. The confidence interval gives a range of values compatible with the unadjusted calculation under its statistical assumptions.

The risk difference is one way to describe a group contrast, not the only one. Relative measures such as risk ratios and odds ratios answer a different question by describing the association on a relative scale. Their interpretation depends on the chosen measure and the event frequency. The posted analysis emphasizes the risk difference for the unadjusted re-calculation, while the sponsor-reported primary test is a Cochran-Mantel-Haenszel comparison.

What does the Cochran-Mantel-Haenszel method do?

The registry identifies the sponsor's primary comparison as Cochran-Mantel-Haenszel. In general, this method can compare categorical outcomes while accounting for strata. The registry record does not specify the stratification variables or provide the full analysis specification, so the particular adjustment used in this trial cannot be described further. The reported p-value should therefore be read as the result of the sponsor's stated method, not as an unadjusted p-value from the displayed group percentages.

A p-value describes how compatible the observed data are with a specified null hypothesis under the test's assumptions. It is not the probability that the null hypothesis is true, nor does it indicate the size or practical importance of a difference. The p-value alone also does not communicate the precision of the estimated effect; the confidence interval provides complementary information about uncertainty in the unadjusted risk-difference estimate.

Why distinguish the reported analysis from a re-calculation?

The posted summary statistics allow a simple unadjusted comparison. That calculation uses the displayed endpoint proportions and group sizes. The registry's reported primary analysis uses Cochran-Mantel-Haenszel, which is a distinct method. Results from these approaches can differ because they do not necessarily use the same information or adjustment. A re-calculation is useful as a transparent check of the posted summaries, but it does not replace the sponsor's analysis of record.

For the primary endpoint, the sponsor reports p = 0.010, while the unadjusted re-calculation reports p = 0.012. The registry does not flag a discrepancy. These values should not be treated as if they came from a single analysis. The method attached to each result is part of its meaning: one is the registry's reported Cochran-Mantel-Haenszel test, and the other is an unadjusted calculation from posted summary statistics.

Why does over-dispersion matter in general?

Over-dispersion is a general concern in some statistical models when the observed variability exceeds what the model assumes. If a model treats observations as less variable or more independent than they are, standard errors can be too small and confidence intervals too narrow. Appropriate modeling can account for extra variability. This issue is not reported as a feature of the primary analysis in this registry record, which reports a categorical comparison; it should not be assumed to have affected this trial.

What is the role of the missing-data rule?

The primary endpoint specifies that participants with missing CDEIS values from endoscopies performed 48 weeks after randomization were counted as non-responders. This is a conservative classification in the sense that missing endpoint status is not counted as success; that general description does not establish that the rule is conservative under every possible data-generating situation. The effect of a missing-data choice depends on why assessments are missing and on the unobserved outcomes those participants might have had.

The registry record does not report the amount or reasons for missing primary endpoint data, or sensitivity analyses under alternative assumptions. It also does not provide enough information to establish whether missingness differed between the groups. Those uncertainties limit assessment of how robust the result is to missing-data assumptions. The specified rule is known, but the information needed to evaluate its consequences fully is not reported in the registry record.

11. Confidence Intervals and Precision

The unadjusted risk-difference estimate for the primary endpoint is -0.156, with a confidence interval from -0.276 to -0.035. A confidence interval is a range generated by a statistical procedure to convey uncertainty around an estimate. In general, narrower intervals indicate greater precision, while wider intervals indicate more uncertainty about the size of the underlying effect. The interval does not include zero, which is consistent with the direction of the observed group percentages under this unadjusted calculation.

The interval describes uncertainty in the re-calculated risk difference, not uncertainty in the sponsor's Cochran-Mantel-Haenszel result. The registry's reported primary analysis gives p = 0.010, but the posted record does not provide a confidence interval for that analysis. It would therefore be inappropriate to present the unadjusted interval as if it were an interval from the sponsor's primary method.

Confidence intervals do not account for every potential source of uncertainty. They do not, by themselves, address open-label conduct, site evaluation of ileocolonoscopies, the missing-data rule, or the possibility of selective emphasis among multiple outcomes. The interval also does not establish that the estimated contrast will recur in another study. It quantifies statistical uncertainty under the assumptions of the particular calculation.

The registry record does not report a confidence interval for the sponsor's primary estimate, and it does not give the stratification details for the Cochran-Mantel-Haenszel analysis. Those omissions limit direct assessment of precision for the sponsor-reported method. The unadjusted confidence interval remains informative as a separate description of the posted summary data, with the distinction between analyses kept explicit.

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 express sample size as participants per arm, not as a total across arms or as a total number of events. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These assumptions describe the planning calculation only; the trial's own original design assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under its assumptions. The 90% power column uses a higher target probability of detection and therefore generally requires more participants per arm. Power is a property of a planned design under assumptions, not a measure of how likely the observed result is to be true.

The rows that plan for 75% or 50% of the observed effect represent smaller effects than the row based on 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm to reach the same target power under the stated assumptions. The illustrations are recalculations based on the observed effect and are not the trial's original sample-size calculation.

These figures are planning illustrations, not observed power. Observed power is not a useful substitute for interpreting the estimated effect and its uncertainty after results are available. The confidence interval and the sponsor's reported analysis are more relevant to understanding the result than a retrospective power figure. No time-to-event endpoint is represented in these primary-endpoint planning illustrations.

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 = 0.459; treatment proportion p₁ = 0.303; average p̄ = 0.381.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6868 = 1.3462.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6780 = 0.5706.
4. n = (1.3462 + 0.5706)² / (-0.1557)² = 151.5, rounded up to 152 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 <- 0.459016393442623                          # control proportion
p1 <- 0.30327868852459                          # 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(1235689)
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 = 152 (80% power), 203 (90% power)
 75% of observed effect: n per arm = 276 (80% power), 368 (90% power)
 50% of observed effect: n per arm = 630 (80% power), 843 (90% power)
power.prop.test: 151.5 
Simulated power at n = 152 per arm: 0.806 (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 reported primary analysis is a Cochran-Mantel-Haenszel superiority test with p = 0.010. The unadjusted re-calculation from the posted group summaries gives a risk difference of -0.156, a confidence interval from -0.276 to -0.035, and p = 0.012. The two results are close, but they come from different analyses and should remain distinct.

The sponsor's method is the registry-reported analysis for the primary endpoint. The unadjusted re-calculation is a transparent comparison of the posted summary statistics; it does not reproduce any stratification that may have been used in the sponsor's analysis. The registry record does not report the strata or enough detail to reconstruct that analysis. The sponsor-reported result should therefore be used when describing the official primary test, while the re-calculation can help readers understand the contrast on an unadjusted risk-difference scale.

The registry does not flag a discrepancy between the reported analysis and the re-calculation. That does not make the methods interchangeable: the reported p-value is tied to the Cochran-Mantel-Haenszel test, and the recalculated p-value is tied to an unadjusted comparison. Neither p-value alone describes the magnitude or clinical importance of the endpoint difference.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns arise when statistical tests are conducted across multiple outcomes or comparisons. As a general matter, the more tests considered, the greater the chance that at least one result will appear notable by chance alone. Researchers can address this through prespecified testing sequences or statistical adjustment, but the registry record does not report a multiplicity adjustment or a detailed testing hierarchy for this study. The primary result is identified as the primary outcome, but the record does not provide enough information to determine how secondary testing was controlled, if at all.

The registry lists 33 outcome measures, 14 analyses, and 32 posted secondary outcome measures. These counts indicate that the record contains more than the primary endpoint, but they do not establish that every listed outcome was tested in the same way or that every result was part of one family of hypotheses. The specific multiplicity plan is not reported in the registry record. Accordingly, secondary p-values should be interpreted with caution and should not be given the same confirmatory status as the primary comparison.

For the primary endpoint, the registry specifies that missing CDEIS values from endoscopies performed 48 weeks after randomization were counted as non-responders. The analysis population is described as all randomized participants. The number of missing assessments, reasons for missingness, and any sensitivity analyses are not reported in the registry record. The rule is explicit, but its impact cannot be fully assessed without those details.

The missing-data handling for the secondary endpoints is not reported in the registry record. The record also does not provide enough detail to establish whether all analyses used the same population, how withdrawals were handled for each outcome, or whether other imputation methods were applied. These gaps make it difficult to assess whether missingness could have affected comparisons or whether the conclusions would be robust to alternative assumptions.

The study was open-label, and the registry says site personnel evaluated the ileocolonoscopies. Whether endpoint readers were masked to group assignment is not reported in the registry record. These features do not determine the direction of any bias, but they are relevant context for interpreting an outcome that depends on endoscopic assessment.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 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 (9.8%), anal abscess (3.3%), abdominal pain (1.6%), ileal stenosis (1.6%), abdominal abscess (1.6%).

The registry reports serious adverse events affecting 25 participants in Clinically Driven Management and 22 participants in Tight Control Management; each group lists 122 participants at risk. Other adverse events affected 78 participants in Clinically Driven Management and 76 participants in Tight Control Management, again with 122 at risk in each group. These are counts of participants affected, not percentages, and the registry's adverse-event summary does not establish that any particular event was caused by a treatment or management strategy.

The most frequently listed serious adverse-event terms include Crohn's disease at 9.8%, anal abscess at 3.3%, and abdominal pain, ileal stenosis, abdominal abscess, and Clostridium difficile infection each at 1.6%. These terms describe events recorded in the registry and should be read in the context of the study population and follow-up. The record does not provide enough detail to assess event timing, duration, severity beyond the serious classification, or relationship to a specific therapy.

Deaths are not reported in the registry record. A count not reported should not be interpreted as evidence that no deaths occurred. The safety summary is descriptive and does not, by itself, determine comparative safety or establish causation.

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

The central statistical result is that the posted percentage meeting the combined endoscopic endpoint was higher in Tight Control Management than in Clinically Driven Management at 48 weeks after randomization. The sponsor's reported Cochran-Mantel-Haenszel analysis gives p = 0.010. The separate unadjusted re-calculation estimates a risk difference of -0.156 for Clinically Driven Management relative to Tight Control Management, with a confidence interval from -0.276 to -0.035. These figures describe the registry's specified endpoint and the analyses identified for it.

The result does not isolate the contribution of a particular drug, because the comparison was between management algorithms and customized therapy could include several medicines. It does not establish how participants experienced symptoms, daily function, or quality of life; those outcomes are not included in the primary endpoint definition. It also does not establish a result for every secondary outcome or for populations not described in the registry.

A statistically notable comparison does not by itself indicate whether the size of the difference is clinically important. That judgment requires clinical context and consideration of the outcome definition, the uncertainty around the estimate, the burdens and risks associated with the strategies, and patient priorities. This statistical summary does not give medical advice or determine which management approach is appropriate for an individual.

Interpretation also depends on the open-label design, site evaluation of endoscopies, and the primary endpoint's rule for missing CDEIS values. The registry does not report the number of missing assessments, alternative missing-data analyses, or whether endpoint readers were masked. The result should therefore be understood as evidence about the recorded randomized comparison under its posted analysis rules, not as a complete account of all possible sources of uncertainty.

The posted secondary findings are directionally consistent with the primary pattern for the displayed outcomes, but multiplicity adjustment is not reported. Those results are less conclusive than the primary comparison. Overall, the registry supports a specific statistical statement about the primary endoscopic endpoint; broader claims about all aspects of disease control, long-term outcomes, or treatment effects are not established by these data alone.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares two strategies for using disease-activity information, rather than testing only a fixed treatment against a control. The strategies differ in the criteria used to guide management: Tight Control Management includes hs-CRP and fecal calprotectin alongside CDAI and corticosteroid use, while Clinically Driven Management uses CDAI and corticosteroid use. That makes the primary contrast relevant to the use of additional monitoring criteria, while also meaning the result cannot be attributed to one medication in isolation.

The primary endpoint combines an endoscopic threshold with the absence of deep ulcerations. This makes the outcome more specific than a single symptom or disease-activity score, but also makes its interpretation depend on the endpoint definition and assessment process. The registry states that site personnel evaluated ileocolonoscopies and that missing CDEIS values were counted as non-responders. Those details are integral to interpreting the reported percentages.

The record also offers a useful contrast between the sponsor's reported Cochran-Mantel-Haenszel test and a simple unadjusted re-calculation from posted summaries. Seeing both emphasizes that an effect estimate and a p-value depend on the method used. The recalculation can describe the absolute contrast transparently, but does not reproduce the registry's reported method.

Finally, the study illustrates why primary and secondary findings should be distinguished. The secondary results broadly follow the primary direction for the displayed outcomes, but the registry does not report multiplicity control. A clear hierarchy of evidence helps readers avoid treating every favorable secondary result as independent confirmation. The missing details about the original sample-size rationale and analysis plan also underscore the importance of separating trial-design information from retrospective planning illustrations.

19. Limitations

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

Several trial-specific limitations affect interpretation. The study was open-label, and the registry reports that ileocolonoscopies were evaluated by the site. Whether the people assessing endoscopic outcomes were masked to assignment is not reported in the registry record. Because the primary endpoint depends on endoscopic classification, the assessment process is relevant to understanding possible measurement influences.

The primary endpoint treats missing CDEIS values at 48 weeks as non-response. The number of missing assessments, reasons for missingness, and results under alternative assumptions are not reported in the registry record. The rule is clear, but its effect on the group comparison cannot be evaluated without those additional details. Missing-data handling for secondary outcomes is also not reported.

The registry reports a sponsor analysis using the Cochran-Mantel-Haenszel method but does not provide the stratification variables or full statistical analysis plan. This limits independent reconstruction of the reported analysis. The unadjusted recalculation is not a substitute for those missing details. The record also does not report the original sample-size justification, interim-analysis plan, or multiplicity adjustment.

The arm descriptions are incomplete, and the interventions were customized. As a result, the registry does not provide enough information in these descriptions to reconstruct the full treatment algorithms or determine the contribution of individual medicines. The record also does not report an endoscopic central-reading procedure. These limitations do not erase the randomized comparison, but they constrain how specifically the result can be interpreted and reproduced.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Two Treatment Algorithms in Adults With Moderate to Severe Crohn's Disease — NCT01235689.
• Registry record last updated 2018-01-16; status last verified 2017-12.
• Results first posted 2017-12-07.
• 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 a completed, randomized, open-label, parallel-group Phase 3 study of adults with moderate to severe Crohn's disease. It compared Tight Control Management, using CDAI, hs-CRP, fecal calprotectin, and corticosteroid-use criteria, with Clinically Driven Management, using CDAI and corticosteroid-use criteria. Customized therapy could include prednisone, adalimumab, and azathioprine.

The primary endpoint was the percentage meeting mucosal healing and no deep ulcerations at 48 weeks after randomization. Missing CDEIS values at that assessment were counted as non-responders. The sponsor reported a Cochran-Mantel-Haenszel superiority analysis with p = 0.010. An unadjusted re-calculation gives a risk difference of -0.156, with a confidence interval from -0.276 to -0.035 and p = 0.012.

The registry also posts secondary results and descriptive safety counts. Multiplicity adjustment, several missing-data details, the original sample-size justification, and the full statistical analysis plan are not reported in the registry record.