Remission in Subjects With Crohn's Disease, 1 Year Phase: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Remission in Subjects With Crohn's Disease, 1 Year Phase (NCT00055497), a randomized phase 3 study. The primary outcome is Number of Randomized Participants Achieving Clinical Remission at Week 56 - Non-Responder Imputation (NRI).

2. Clinical Question

3. Trial Design

This was a completed phase 3, randomized, double-blind, placebo-controlled, parallel-group trial sponsored by Abbott. The record lists 276 enrollees and describes the trial as quadruple-masked. Its stated aim was to evaluate maintenance of clinical remission up to 56 weeks among participants with Crohn's disease who had participated in NCT00055523, and to delineate safety during treatment up to 56 weeks. The registry record does not provide the original sample-size justification or the detailed sequence by which participants entered the randomized treatment groups.

The primary outcome comparison includes three double-blind groups: placebo, adalimumab 40 mg every other week, and adalimumab 40 mg every week. The analyzed groups contain 18, 19, and 18 participants, respectively. This is a narrower set of groups than the total enrollment figure. An open-label adalimumab group is also listed, with 221 participants in the safety results and 204 in one posted Week 24 outcome; its treatment was 40 mg every other week or every week. The record does not explain the differences in group sizes across outcomes, so these should not be interpreted as evidence about why participants were included or excluded.

The primary endpoint was assessed at Week 56 and used non-responder imputation for missing data. Secondary outcomes include clinical remission at Week 24 under non-responder imputation and last observation carried forward, Week 56 remission in open-label participants, and clinical response measures. The registry record lists these outcomes but does not report a complete statistical protocol for their analysis. In particular, it does not report the trial's original sample-size assumptions, prespecified multiplicity strategy, or detailed handling of all analysis populations. These absences limit how closely the posted results can be mapped to an intended confirmatory analysis.

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: Study was rollover of NCT00055523; screening done in NCT00055523. At Week 4 of NCT00055497, 55 remitters at Week 0 and Week 4 of Study NCT00055497 were randomized to DB therapy; 204 non-remitters were assigned to OL adalimumab. 17 discontinued before/at Week 4, included in OL group for Participant Flow and AEs because they were not randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants randomized to DB treatment who received at least one injection of blinded study drug were included in assigned treatment group. Nonresponder imputation (NRI) (clinical remission not achieved) was used for missing data.

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 Number of Randomized Participants Achieving Clinical Remission at Week 56 - Non-Responder Imputation (NRI), measured over Week 56.

The primary endpoint counted randomized participants who achieved clinical remission at Week 56. Remission was defined as a CDAI score <150. The CDAI combines eight Crohn's-related variables assessed over a one-week period. The registry description states that scores range from 0 to 633 in this trial and its lead-in study, with a lower score indicating less severe disease activity.

A threshold-based outcome turns a clinical activity measure into a binary result: each participant either meets the stated remission definition or does not. Counting participants who cross the threshold gives an interpretable comparison of the proportion meeting the endpoint in each treatment group. It does not, by itself, describe changes in CDAI among participants who remain on the same side of the threshold, nor the timing of changes during follow-up. Those are distinct questions from whether remission was achieved at the specified assessment.

The endpoint uses non-responder imputation. Under the registry's description, missing primary outcome data were counted as clinical remission not achieved. This rule preserves participants in the assigned treatment group while making an explicit assumption about missing outcomes. It can affect the estimated group results if outcome availability differs across groups or if missing participants would otherwise have had different remission outcomes. The record does not provide enough detail to assess those possibilities. The endpoint was chosen to address maintenance of clinical remission through Week 56, but it should be read as a specific Week 56 status under the stated imputation rule, not as a complete account of each participant's course over the full follow-up period.

7. Results Posted in the Registry

• DB Adalimumab 40 mg Every Other Week (Eow): 47.4% (9/19) versus 33.3% (6/18) on control; risk difference 14.0 percentage points (95% CI -17.2 to 45.3), risk ratio 1.42 (0.63–3.19); unadjusted two-proportion z-test p = 0.385.
• DB Adalimumab 40 mg Every Week (ew): 66.7% (12/18) versus 33.3% (6/18) on control; risk difference 33.3 percentage points (95% CI 2.5 to 64.1), risk ratio 2.00 (0.96–4.15); unadjusted two-proportion z-test p = 0.046.

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.

Number of Participants Achieving Clinical Remission at Week 24 - NRI

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • DB Adalimumab 40 mg Every Other Week (Eow): 57.9% (11/19) versus 38.9% (7/18) on control; risk difference 19.0 percentage points (95% CI -12.6 to 50.6), risk ratio 1.49 (0.74–2.98); unadjusted two-proportion z-test p = 0.248.
  • DB Adalimumab 40 mg Every Week (ew): 94.4% (17/18) versus 38.9% (7/18) on control; risk difference 55.6 percentage points (95% CI 30.7 to 80.4), risk ratio 2.43 (1.35–4.38); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DB Adalimumab 40 mg Every Other Week (Eow) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for DB Adalimumab 40 mg Every Week (ew) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants Achieving Clinical Remission at Week 24 - LOCF

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • DB Adalimumab 40 mg Every Other Week (Eow): 57.9% (11/19) versus 38.9% (7/18) on control; risk difference 19.0 percentage points (95% CI -12.6 to 50.6), risk ratio 1.49 (0.74–2.98); unadjusted two-proportion z-test p = 0.248.
  • DB Adalimumab 40 mg Every Week (ew): 94.4% (17/18) versus 38.9% (7/18) on control; risk difference 55.6 percentage points (95% CI 30.7 to 80.4), risk ratio 2.43 (1.35–4.38); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DB Adalimumab 40 mg Every Other Week (Eow) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for DB Adalimumab 40 mg Every Week (ew) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes covering Week 24 clinical remission, Week 56 remission among open-label participants, and clinical response measures. For Week 24, results are listed under both non-responder imputation and last observation carried forward. The posted Week 24 group pattern broadly points in the same direction as the primary Week 56 counts: the active double-blind groups have higher remission counts than placebo, and the every-week group has the largest count among those randomized groups. This directional resemblance is useful context, but it does not make the secondary outcomes independent confirmation of the primary result.

Different assessment weeks and imputation rules answer related but nonidentical questions. Week 24 status is not the same endpoint as Week 56 status, and last observation carried forward does not impose the same missing-data assumption as non-responder imputation. The open-label outcomes also differ from the randomized double-blind comparison. Results from an open-label group should not be interpreted as a direct randomized contrast against placebo on the basis of these counts.

The registry includes recalculated comparisons for the posted Week 24 results, but those are unadjusted. When multiple outcomes, time points, and treatment contrasts are examined, some apparently notable results can occur by chance even when there is no corresponding underlying effect. In general, multiplicity adjustments or a prespecified hierarchy can control how repeated testing is interpreted; the registry record does not report such a strategy. Therefore, secondary findings carry less weight than a clearly specified primary analysis, especially when the trial's full statistical plan is unavailable.

The secondary outcome list also includes clinical response measures and Week 56 outcomes in open-label participants. Their results are not reported in the registry record. The available secondary results offer context about outcome patterns and the sensitivity of findings to imputation, but they do not resolve the difference between the sponsor's reported primary test and the recalculated pairwise contrasts. They should be understood as supportive descriptions rather than a basis for a separate confirmatory conclusion.

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

• Number of Participants Achieving Clinical Remission at Week 24 - NRI
• Number of OL Participants Achieving Clinical Remission at Week 56 - NRI
• Number of Participants Achieving Clinical Response 100 (CR-100) - NRI
• Number of Participants Achieving Clinical Response 70 (CR-70)- NRI
• Number of Participants Achieving Clinical Remission at Week 24 - LOCF
• Number of OL Participants Achieving Clinical Remission at Week 56 - LOCF
• Number of Participants Achieving CR-100 - LOCF
• Number of Participants Achieving CR-70 - LOCF

9. Statistical Interpretation

10. Statistical Methods Explained

Clinical trial results for binary outcomes can be described as counts and as proportions. Here, the endpoint is a count of participants meeting a remission definition, while the denominators show the number in each group for the primary analysis. The associated proportion expresses the count relative to its group size. A comparison can then be expressed as a risk difference: the estimated proportion in one group minus the estimated proportion in the comparator group. A positive risk difference means the observed proportion was higher in the named treatment group; a negative value means it was lower. This is a descriptive contrast and does not, on its own, establish a causal or clinically important effect.

What does a confidence interval describe?

A confidence interval gives a range of values compatible with the data under the method used to calculate it. It communicates uncertainty around an estimate rather than a guarantee that the true effect lies inside that particular interval. Wider intervals indicate less precision. With small group sizes and binary outcomes, estimates can be sensitive to the outcomes of a few participants, so the interval is important context for the point estimate.

For every-other-week treatment versus placebo, the recalculated risk difference is 0.140 and the 95% confidence interval is -0.172 to 0.453. For every-week treatment versus placebo, the recalculated risk difference is 0.333 and the 95% confidence interval is 0.025 to 0.641. These intervals correspond to unadjusted pairwise recalculations from the posted summary counts. They are not the sponsor's reported three-group analysis. The registry does not state the original protocol's planned contrast or whether the recalculated interval method matches the sponsor's intended method.

How should p-values be read?

A p-value summarizes how surprising data at least as incompatible with a null hypothesis would be under the assumptions of a specified statistical test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The pairwise recalculated p-values are 0.385 for every-other-week treatment and 0.046 for every-week treatment, each compared with placebo. They are unadjusted, so they do not account for testing multiple comparisons or outcomes. The registry-reported Log Rank p-value of 0.142 applies to the three primary groups together and should be kept separate from the pairwise recalculated p-values.

Risk ratios and odds ratios are alternative ways to express binary-outcome contrasts. A risk ratio compares the proportions directly; an odds ratio compares the odds of the event. They can differ in magnitude and interpretation, particularly when outcomes are common. The posted recalculations include these measures, but the risk difference is useful for reading absolute contrasts. None of these measures removes the uncertainty associated with the small primary groups. Measures also depend on the endpoint definition and on the missing-data rule, so the primary non-responder-imputed result should not be conflated with secondary analyses using another rule.

Why can an overall test differ from pairwise contrasts?

An overall test addresses a different statistical question from separate comparisons of each active group against placebo. A Log Rank test is a method generally used to compare time-to-event patterns. In general, it uses event timing information and may account for the pattern of events over follow-up, whereas a comparison of binary counts at one specified time contrasts endpoint status at that time. The registry reports the Log Rank method and p = 0.142, but it does not provide the event-time data or enough detail to reconstruct that test. The primary endpoint is described as a Week 56 count, so the relationship between the reported Log Rank analysis and that endpoint is not fully explained in the registry record.

In general, over-dispersion matters when outcome variability is greater than a statistical model expects. It can make standard errors too small and confidence intervals too narrow if ignored. The posted primary endpoint is binary and the record does not report an over-dispersion adjustment; no claim about such an adjustment can be made. For binary counts in small groups, the important practical concerns are the wide uncertainty, the exact handling of missing observations, the analysis method, and the number of comparisons examined. The registry record does not report a complete statistical plan addressing those concerns.

What does imputation change?

Non-responder imputation classifies missing outcomes as failure to achieve the endpoint, as stated in the primary outcome description. Last observation carried forward, used for some secondary results, instead carries a participant's last recorded outcome forward to the later assessment. These approaches make different assumptions about missing follow-up. In general, neither method can recover an unobserved outcome with certainty. A result may depend on which rule is applied, so outcomes using non-responder imputation and last observation carried forward should be identified separately rather than combined as though they were identical analyses.

The calculations labeled as recalculations are unadjusted comparisons derived from the posted group counts and denominators. They offer a transparent way to describe the observed differences, but they are not a substitute for the sponsor's analysis. The registry record does not report the full protocol-level analysis plan, the original sample-size justification, or a complete account of how the sponsor handled every endpoint and analysis population. These missing details constrain interpretation of both the estimates and the reported tests.

11. Confidence Intervals and Precision

The primary group sizes are small: 18 participants for placebo, 19 for every-other-week adalimumab, and 18 for every-week adalimumab. With binary outcomes in groups of this size, a small change in the number meeting the endpoint can noticeably shift the estimated proportion and comparison. Confidence intervals make this sampling uncertainty visible. They are more informative than a point estimate alone because they show a range of effects consistent with the observed data under the recalculation method.

For the every-other-week comparison, the risk-difference interval runs from -0.172 to 0.453. It spans zero and includes values in both directions. Thus the posted counts do not give a precise estimate of the direction of this pairwise contrast. For the every-week comparison, the interval runs from 0.025 to 0.641. It lies above zero, but its width still allows a broad range of positive contrasts. The point estimate of 0.333 should not be read as known with that exact precision.

These intervals belong to unadjusted recalculations, not to the sponsor-reported Log Rank analysis. The registry's reported three-group result is p = 0.142 and does not include a confidence interval in the posted analysis. The registry record does not report the sponsor's confidence intervals for the primary comparison. That distinction matters: precision cannot be inferred from a p-value alone, and a p-value from one method cannot be used as though it were the interval estimate from another.

The interval widths also reflect only the calculation and data described. They do not capture uncertainty about the suitability of the endpoint definition, missing-data assumptions, multiplicity, or possible differences between the planned analysis and the posted results. Non-responder imputation makes missing primary observations count as non-remission, but the record does not show how many observations were missing in each group. Consequently, the precision of the observed estimates can be discussed, while the effect of missingness on those estimates remains unclear.

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.

Sample-size figures in the planning illustrations are participants per arm, not total participants across the trial. They are calculated for a two-arm comparison and are not the trial's original enrollment target or the primary analysis group sizes. The original design assumptions and the trial's own sample-size justification are not reported in the registry record.

The planning assumptions listed are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses a stated fraction of the observed effect as the effect to detect. The rows labeled as planning for 100%, 75%, or 50% of the observed effect therefore illustrate how the required group size changes when the target effect is set to different fractions of the observed contrast.

The 80% power column gives the estimated number of participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect is the true one. The 90% power column gives the corresponding per-arm number for a design with a 90% chance under the same assumptions. For example, at 100% of the observed effect, the every-other-week comparison lists 191 participants per arm for 80% power and 255 for 90% power; the every-week comparison lists 35 and 46, respectively. These illustrations are sensitive to the observed effect: a smaller target effect requires more participants per arm. The planning counts are not observed power.

These estimates are planning illustrations rather than evidence that the trial was adequately or inadequately sized. They use the observed contrast as an input, and observed effects from small groups can be unstable. They also rely on the stated approximation and assumptions, which may not represent the trial's actual design or analysis. The figures should be read as conditional planning calculations, not as a reconstruction of the trial's original design process.

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 = 0.333; treatment proportion p₁ = 0.474; average p̄ = 0.404.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6938 = 1.3599.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6867 = 0.5779.
4. n = (1.3599 + 0.5779)² / (0.1404)² = 190.6, rounded up to 191 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 <- 0.333333333333333                          # control proportion
p1 <- 0.473684210526316                          # 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(55497)
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 = 191 (80% power), 255 (90% power)
 75% of observed effect: n per arm = 335 (80% power), 448 (90% power)
 50% of observed effect: n per arm = 741 (80% power), 991 (90% power)
power.prop.test: 190.6 
Simulated power at n = 191 per arm: 0.807 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports a sponsor analysis using the Log Rank method across the three primary groups, with p = 0.142. It does not post a corresponding parameter estimate or confidence interval. The recalculations compare each adalimumab schedule with placebo using the Week 56 counts and denominators. Those calculations give risk differences and unadjusted p-values, but they are not the same analysis as the sponsor-reported three-group Log Rank test.

The record flags a discrepancy, so the sponsor's own analysis takes precedence. This does not mean that the recalculated contrasts should be ignored: they describe the posted counts in a transparent, unadjusted way and provide confidence intervals for those pairwise comparisons. Rather, the recalculations should not be presented as though they were the trial's reported primary analysis, nor should their p-values be used to replace the sponsor's result. The overall test and the pairwise contrasts address different questions and use different methods.

The registry record does not report enough detail to reconcile the two analyses, including the full analysis plan and the information used in the Log Rank test. It is therefore not possible to determine from the posted record whether the discrepancy reflects a different endpoint representation, analysis population, or another methodological choice. Interpretation should retain both details: the sponsor-reported overall result is p = 0.142, and the posted counts yield unadjusted pairwise recalculations with their own uncertainty.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when researchers test several treatment contrasts, outcomes, or assessment times. The more tests considered, the greater the chance that at least one result will appear statistically notable by chance. The primary outcome has two pairwise recalculations against placebo, and the registry also lists multiple secondary outcomes, including remission at different times, more than one missing-data approach, and clinical response measures. The pairwise recalculated p-values are unadjusted. The registry record does not report a prespecified adjustment, testing hierarchy, or other multiplicity strategy for the trial.

The sponsor-reported primary analysis is a Log Rank test across the three groups, with p = 0.142. The record does not explain how this overall analysis related to the pairwise comparisons or to the other outcomes. Without a reported analysis plan, it is not possible to determine which comparisons were intended to be confirmatory, whether any analyses were exploratory, or how the sponsor controlled interpretation across repeated tests. This is one reason not to treat an isolated unadjusted pairwise result as definitive.

Missing data are handled explicitly for the primary endpoint: non-responder imputation counts missing clinical remission outcomes as not achieved. Some secondary Week 24 results use last observation carried forward instead. These approaches embody different assumptions. The record does not report the number of missing primary outcomes by group, the reasons for missingness, or sensitivity analyses testing alternative assumptions. It also does not state a complete missing-data plan for every outcome.

The primary population is described as participants randomized to double-blind treatment who received at least one injection, analyzed in their assigned treatment group. This definition clarifies the posted primary analysis population, but the registry record does not give enough information to assess all exclusions or the completeness of follow-up. The record's total enrollment and outcome-specific group sizes should not be treated as interchangeable denominators. Taken together, the unreported multiplicity and missing-data details limit confidence in broad claims based on any single p-value, even when the endpoint and group counts are clearly stated.

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: back pain (5.6%), ileal stenosis (5.6%), small intestinal obstruction (5.6%), coronary artery disease (5.3%), crohn's disease (4.1%).

The serious adverse event counts in the double-blind groups were 2 of 18 participants with placebo, 1 of 19 with adalimumab every other week, and 0 of 18 with adalimumab every week. The open-label adalimumab group had 37 serious adverse events among 221 participants at risk. These are counts reported for the groups; they do not by themselves establish whether an event was caused by treatment or how the groups compare under a prespecified safety analysis.

The registry also lists serious adverse event terms with percentages, including back pain, ileal stenosis, small intestinal obstruction, coronary artery disease, Crohn's disease, and abdominal abscess. The listed values should be read as registry entries, not as a complete account of all possible adverse events. The record does not provide deaths for these groups; deaths are not reported in the registry record. It also does not give enough detail in the posted safety summary to interpret event timing, exposure duration by group, or causal assessment. Safety counts therefore describe reported events and at-risk group sizes, rather than proving that a treatment caused or prevented an event.

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

The primary endpoint records whether participants met a stated clinical remission threshold at Week 56, with missing data counted as failure to achieve remission. The registry counts show more participants meeting that definition in each adalimumab group than in the placebo group, and the every-week group has the largest count. The pairwise recalculations attach considerable uncertainty to these observations. The sponsor-reported three-group Log Rank analysis gives p = 0.142, and the registry record flags a discrepancy between that result and the recalculated contrasts.

These results do not establish that every participant would have the same outcome, nor do they quantify the full course of disease activity during follow-up. A binary Week 56 endpoint compresses a clinical measure into a threshold classification. It does not show the amount of change in CDAI among participants who did not cross the threshold, the duration of remission, or the timing of individual outcomes. Those questions are not answered by the posted primary counts.

The primary result also depends on non-responder imputation. Missing observations are counted as not achieving remission, but the registry does not state how many observations were missing in each group or how results might change under other assumptions. Secondary results use different times and, in some cases, last observation carried forward. Differences among those results may reflect the endpoint, follow-up time, or imputation method as well as the treatment comparison.

The available information supports a statistical description of the trial record: the observed counts, the recalculated risk differences and confidence intervals, and the sponsor's reported test. It does not support medical advice or a conclusion about whether an individual should receive a treatment. Nor does a p-value alone establish clinical importance, and the unadjusted recalculations should not displace the sponsor's reported analysis. The registry record leaves important design and analysis details unreported, so conclusions should remain specific to these participants, this endpoint, and the posted analysis.

18. Why This Trial Matters Statistically

This trial is statistically informative because it brings together several issues that often matter in clinical research: a binary endpoint, small randomized groups in the primary comparison, missing-data imputation, multiple secondary outcomes, and a difference between the sponsor-reported analysis and unadjusted recalculations. Each issue changes how an estimate should be read. The group counts are straightforward, but the inferential picture depends on the analysis method and its assumptions.

The confidence intervals make clear that the recalculated pairwise contrasts are not equally precise and that the every-other-week contrast is compatible with effects in either direction. The every-week interval is above zero in the recalculation, but remains wide. In parallel, the sponsor's Log Rank test across all three groups reports p = 0.142. Keeping these results distinct is an important statistical practice: a recalculation can describe posted summary data without replacing the trial's own analysis.

The record also illustrates why endpoint definitions and missing-data rules belong alongside treatment counts. Non-responder imputation gives a clear rule for missing primary outcomes, while some secondary outcomes use last observation carried forward. Those choices define what is being estimated and can influence the resulting pattern. Without the numbers missing by group or sensitivity analyses, the effect of those assumptions cannot be assessed from the registry record.

Finally, the planning illustrations show how sample-size calculations depend on the target effect and assumptions, rather than functioning as a retrospective verdict on the original trial. The trial's own sample-size justification is not reported. Taken together, these details make the record useful for learning how to separate observed data, recalculated contrasts, sponsor-reported tests, and design information that is not available.

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.

The primary randomized groups are small, and the confidence intervals around the recalculated risk differences are broad. This limits precision and makes the estimated contrasts sensitive to a small number of participant outcomes. The discrepancy flag is consequential: the sponsor-reported Log Rank test differs from the pairwise calculations based on the Week 56 counts, and the registry record does not provide enough information to reconcile the analyses.

The record does not report the original sample-size justification, detailed eligibility criteria, or a complete statistical analysis plan. It also does not state the prespecified multiplicity approach or provide a full explanation of the relationship between the primary Week 56 endpoint and the Log Rank analysis. These omissions make it difficult to judge whether the posted comparisons align with the intended confirmatory analysis.

Missing-data information is limited. The primary endpoint uses non-responder imputation, but the number and distribution of missing observations are not reported in the record. Some secondary outcomes use last observation carried forward, and the impact of this alternative assumption is not fully assessed. Outcome-specific group sizes vary, including the open-label group, and the record does not explain those differences.

The open-label group is not part of the randomized primary comparison, so its results do not have the same interpretive basis as the double-blind groups. Secondary outcomes cover multiple times, measures, and imputation methods, while results for some listed outcomes are not reported in the registry record. Finally, serious adverse event counts alone do not establish causality or provide a complete safety comparison. These limitations call for conclusions focused on the posted data and the specific analyses described, rather than broad generalization.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Remission in Subjects With Crohn's Disease, 1 Year Phase — NCT00055497.
• Registry record last updated 2011-04-11; status last verified 2011-04.
• Results first posted 2010-05-18.
• 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

NCT00055497 is a completed phase 3 randomized, quadruple-masked, parallel-group, placebo-controlled study sponsored by Abbott. It enrolled 276 participants and examined adalimumab for maintenance of clinical remission in Crohn's disease through 56 weeks. The primary endpoint was the number achieving remission at Week 56, defined as CDAI <150, with missing outcomes treated as non-remission under non-responder imputation.

The primary counts were 6 of 18 for placebo, 9 of 19 for every-other-week adalimumab, and 12 of 18 for every-week adalimumab. The sponsor-reported three-group Log Rank analysis had p = 0.142. Unadjusted pairwise recalculations provide risk differences and confidence intervals but are flagged as discrepant, so the sponsor's own analysis takes precedence. Missing-data, multiplicity, and original sample-size details are not fully reported in the registry record.