A Study of the Efficacy and Safety of Adalimumab in Pediatric Subjects With Enthesitis Related Arthritis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of the Efficacy and Safety of Adalimumab in Pediatric Subjects With Enthesitis Related Arthritis (NCT01166282), a randomized phase 3 study. The primary outcome is Percent Change in Number of Active Joints With Arthritis From Baseline to Week 12.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, quadruple-masked phase 3 study of adalimumab and placebo in pediatric subjects with Enthesitis Related Arthritis. The official title describes it as a double-blind, placebo-controlled, multicenter study. The registry record lists AbbVie (prior sponsor, Abbott) as sponsor and enrollment of 46. The study is marked completed, with a start date of 2010-09 and primary completion in 2012-11.

During the double-blind period, one group received placebo for adalimumab every other week for 12 weeks. The other received adalimumab every other week for 12 weeks, with body-surface-area dosing of 24 mg/m^2 up to a maximum of 40 mg. The record additionally lists an open-label adalimumab group receiving the same dosing schedule for up to 192 weeks. Details of how participants entered or proceeded into that open-label period are not reported in the registry record, so its relationship to the randomized comparison should not be inferred from the group label alone.

The stated study purpose was to evaluate the efficacy and safety of adalimumab given subcutaneously every other week compared with placebo. The principal randomized comparison presented for the primary outcome is at Week 12. The registry record names the ITT population for that outcome and says last observation carried forward was used for missing primary-outcome data. The original sample-size justification, intended analysis plan, and any interim-analysis plan 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.

Double-blind Period

Open-label Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT population

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: Intent-to-treat (ITT) population: All randomized participants who received at least 1 dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Percent Change in Number of Active Joints With Arthritis From Baseline to Week 12, measured over Baseline and Week 12.

The primary endpoint was percent change in the number of active joints with arthritis from baseline to Week 12. The assessment recorded the number of active joints, with a total possible score from 0, meaning no active joints, to 72, meaning all active joints. A joint was assessed for swelling not due to deformity or for loss of motion together with pain and/or tenderness. Baseline was defined as the last nonmissing value before the first dose of study drug.

Change in an active-joint count is a continuous measure: it can represent a range of values rather than only whether a participant did or did not meet a response threshold. The endpoint’s percent-change scale expresses change relative to baseline, while the reported group summaries are means with standard deviations. A negative percent change indicates a lower active-joint count relative to baseline; it does not by itself describe every participant’s course.

Such a measure is used to describe change in a clinical feature of the condition across the study period and to compare group averages. The record states that last observation carried forward was used for missing primary-outcome data and that the analysis population was ITT. The exact handling of all other analysis details is not reported in the registry record.

7. Results Posted in the Registry

• Double-blind Adalimumab EOW: mean -62.60 versus -11.60 on control; difference -51.00 (95% CI -106.01 to 4.01), standardized effect d = -0.68; z-test p = 0.069.

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 Achieving Pediatric American College of Rheumatology Pediatric 30% Response (ACR Pedi30)

• 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:
  • Double-blind Adalimumab EOW: 71.0% (22/31) versus 60.0% (9/15) on control; risk difference 11.0 percentage points (95% CI -18.5 to 40.5), risk ratio 1.18 (0.74–1.89); unadjusted two-proportion z-test p = 0.457.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind Adalimumab EOW and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Achieving Pediatric American College of Rheumatology Pediatric 50% Response (ACR Pedi50)

• 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:
  • Double-blind Adalimumab EOW: 67.7% (21/31) versus 40.0% (6/15) on control; risk difference 27.7 percentage points (95% CI -2.0 to 57.5), risk ratio 1.69 (0.87–3.30); unadjusted two-proportion z-test p = 0.073.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Double-blind Adalimumab EOW and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Achieving Pediatric American College of Rheumatology Pediatric 70% Response (ACR Pedi70)

• 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:
  • Double-blind Adalimumab EOW: 54.8% (17/31) versus 20.0% (3/15) on control; risk difference 34.8 percentage points (95% CI 8.1 to 61.6), risk ratio 2.74 (0.95–7.92); unadjusted two-proportion z-test p = 0.025.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Double-blind Adalimumab EOW than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the posted ACR response outcomes, the group summaries are directionally more favorable in the adalimumab group than in the placebo group, with the contrast varying across response thresholds. The inferential picture is not uniform: the re-calculated intervals for some thresholds include zero, while the interval for the highest listed threshold does not. These results add context to the primary active-joint endpoint, but they are not the same measure and should not be treated as interchangeable evidence.

The registry also lists change in sites of enthesitis, tender joint count, swollen joint count, and adverse events among secondary outcomes. Numerical results for the enthesitis and joint-count outcomes are not reported in the registry record. The secondary outcomes list and the number of posted outcome measures do not establish that all listed results are available for interpretation.

Secondary endpoints can help describe different aspects of a condition and can provide supportive evidence, but multiple comparisons raise the chance of observing an apparently notable result by chance. The registry record does not report a multiplicity adjustment or a hierarchy for these secondary tests. Accordingly, unadjusted secondary p-values and intervals carry less weight than the prespecified primary comparison when drawing an overall statistical conclusion. Their pattern may be informative, but it should not be used to override the primary result or to claim independent confirmation.

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

• Number of Sites of Enthesitis: Change From Baseline to Week 12
• Tender Joint Count (TJC72): Change From Baseline to Week 12
• Swollen Joint Count (SJC68): Change From Baseline to Week 12
• Percentage of Participants Achieving Pediatric American College of Rheumatology Pediatric 30% Response (ACR Pedi30)
• Percentage of Participants Achieving Pediatric American College of Rheumatology Pediatric 50% Response (ACR Pedi50)
• Percentage of Participants Achieving Pediatric American College of Rheumatology Pediatric 70% Response (ACR Pedi70)
• Number of Participants With Adverse Events (AEs)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a mean percent change in active-joint count. A comparison of means summarizes the difference between the groups’ average values. The sign depends on the order of the groups used in the contrast. For the recalculated comparison, the mean difference is expressed as adalimumab relative to placebo, so a negative value corresponds to a more negative mean change in the adalimumab group.

What does the confidence interval describe?

A confidence interval describes the uncertainty around an estimated group difference under the method used to calculate it. A narrower interval indicates greater precision, while a wider interval allows a broader range of plausible differences. An interval that includes zero is compatible with no group difference under that analysis; an interval entirely on one side of zero is not. These interpretations concern the particular estimate and method, not certainty about an individual participant’s result.

The reported sponsor analysis is an ANCOVA of final values. In general, analysis of covariance compares group outcomes while accounting for specified covariates. The registry record does not name the covariates or provide enough detail to reconstruct the fitted model. The reported estimate and confidence interval should therefore be understood as the registry’s stated ANCOVA result, rather than as a model that can be independently recreated from the posted arm means and standard deviations.

Why do the recalculation and registry analysis differ?

The recalculated mean difference is a simple, unadjusted comparison based on the posted summary statistics. It is not the same analysis as ANCOVA. Different analysis methods can yield different estimates and uncertainty because they use information and assumptions differently. The registry record does not provide the detail needed to identify which specific feature explains the difference in this trial. Since the discrepancy is present, the sponsor’s own analysis takes precedence; the re-calculation remains useful as a transparent, unadjusted reference, not as a replacement.

The primary outcome reports mean and standard deviation. A standard deviation describes how dispersed participant-level values are around the group mean; it is not the uncertainty in the mean itself. The standard error, by contrast, represents uncertainty in an estimated mean. Both measures are relevant to precision, but they answer different questions. The reported arm summaries show substantial variability, especially in the placebo group, which is relevant when considering how much information the small randomized comparison can provide.

How should binary response outcomes be understood?

The ACR Pedi30, ACR Pedi50, and ACR Pedi70 outcomes are percentages of participants meeting response criteria. A risk difference compares the response proportions between groups by subtraction, while a risk ratio compares them by division. An odds ratio compares the odds of response. These measures use different scales, and their numerical values are not directly interchangeable. The recalculated risk-difference intervals describe uncertainty around the difference in response proportions; they do not show that every participant in one group had a better outcome than every participant in the other.

For a binary endpoint with small group sizes, the number of participants meeting the criterion matters as well as the percentage. The registry’s reported secondary analyses use Fisher Exact, a method suitable for tests of association in categorical data, including settings with small cell counts. The posted re-calculated p-values and intervals are unadjusted. A small p-value does not measure the size or clinical importance of an effect, and a larger p-value does not establish that groups are equivalent.

Why can over-dispersion matter?

Over-dispersion is a general issue for count or response data when the observed variation is larger than a model assumes. If a method understates variability, its standard errors can be too small and its intervals too narrow. The primary endpoint is reported as a continuous percent change with a standard deviation, rather than as a count-model analysis. The registry record does not report a model-based variance assessment or an over-dispersion analysis, so no trial-specific conclusion about over-dispersion can be drawn. In general, checking whether the assumed variation is appropriate is important when interpreting model-based uncertainty.

The primary analysis population is identified as ITT, and LOCF was used for missing primary values. ITT generally aims to analyze participants according to their randomized group, preserving the comparison created by random allocation. LOCF carries a participant’s last observed value forward to represent a later missing value. This is a specific imputation approach; it does not remove uncertainty about what the missing value would have been. The registry record does not state sensitivity analyses or the missing-data procedures for secondary outcomes.

11. Confidence Intervals and Precision

The primary endpoint’s re-calculated mean difference is -51.0, with a confidence interval from -106.0 to 4.007. Its width reflects considerable uncertainty around the unadjusted contrast, including values on either side of zero. The reported standard deviations are 100.5 for placebo and 59.53 for adalimumab, indicating substantial variation in participant-level percent changes relative to the group means. The registry-reported ANCOVA estimate is -51.17, with a 95% confidence interval from -99.69 to -2.66. These intervals arise from different analyses and should be interpreted separately.

For the secondary binary outcomes, the confidence intervals also indicate varying degrees of precision. The posted ACR Pedi30 and Pedi50 risk-difference intervals include zero, while the Pedi70 interval is above zero. These are unadjusted recalculated intervals, and the sponsor-reported Fisher Exact analyses give their own confidence intervals and p-values. The registry does not report a multiplicity adjustment, which matters when considering a set of secondary comparisons rather than one prespecified test in isolation.

Confidence intervals do not give the probability that the true effect lies inside a particular calculated interval. Rather, in general, they express the uncertainty produced by a statistical procedure under its assumptions. Precision depends on factors such as the amount of information, variability, and analysis method. With the relatively small randomized groups in this study, the estimates can remain uncertain even when the point estimate appears sizable. The trial’s own precision targets or design assumptions are not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total participants or total events. They are illustrations based on the observed effect, not the trial’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial’s sample-size assumptions are not reported in the registry record.

The 80% power column describes the planned number of participants per arm under those assumptions for a hypothetical study to have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses a higher target chance of detection under the same stated planning framework. These are design-planning quantities, not guarantees about results. The figures are illustrations only and do not describe the power achieved by this completed trial.

Rows that plan for a smaller fraction of the observed effect require more participants per arm. This is expected: smaller differences are harder to distinguish from random variation, all else being equal. The figures are tied to the observed effect in this study, so they should not be treated as a validated estimate of the effect in another population or as a substitute for a prospectively specified design calculation. The planning values do not incorporate a trial-specific account of missing data, multiplicity, or other design considerations unless stated in the planning assumptions.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -51.000; pooled standard deviation σ = 75.033.
2. n = 2 × (1.96 + 0.842)² × 75.033² / -51.000² = 34.0, rounded up to 34 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
delta <- -51                      # observed difference in means
sigma <- 75.0330422668452                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1166282)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 34 (80% power), 46 (90% power)
 75% of observed effect: n per arm = 61 (80% power), 81 (90% power)
 50% of observed effect: n per arm = 136 (80% power), 182 (90% power)
power.t.test: 35 
Simulated power at n = 34 per arm: 0.789 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 ANCOVA for the primary comparison. It gives a mean difference in final values of -51.17, a 95% confidence interval from -99.69 to -2.66, and p =0.039. The recalculated comparison is a simple unadjusted analysis of posted summary statistics and gives a mean difference of -51.0, a confidence interval from -106.0 to 4.007, and p = 0.069.

These are not identical estimates from the same model. The recalculation does not reproduce the sponsor’s ANCOVA, and the registry record does not report enough model detail to determine why their intervals and p-values differ. Because the discrepancy is true, the sponsor’s own analysis takes precedence for interpreting the trial’s reported primary result. The unadjusted recalculation remains a supplementary check on the arm summaries, not an alternative sponsor result.

For secondary response outcomes, the registry lists Fisher Exact analyses. Their reported estimates, intervals, and p-values need to be distinguished from the separate unadjusted recalculations. The registry record does not state whether the reported sponsor analyses account for multiplicity across outcomes.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary endpoint and lists multiple secondary outcomes, including several response thresholds and joint assessments. It does not report a multiplicity-control procedure, a hierarchy among secondary outcomes, or a detailed statistical analysis plan. When several outcomes are tested, the chance of at least one seemingly notable result can rise unless the analysis accounts for the family of comparisons. The posted unadjusted secondary results should therefore be interpreted cautiously and as exploratory or supportive rather than as a set of independent confirmatory findings.

For the primary endpoint, the record identifies the ITT population and states that last observation carried forward was used for missing values. LOCF substitutes the last nonmissing observation for a later missing measurement. In general, this can simplify analysis but may not reflect the participant’s unobserved outcome at the target time. The record does not report a sensitivity analysis using alternative missing-data assumptions, or details about the amount and pattern of missing primary data.

Handling of missing data for the secondary outcomes is not reported in the registry record. The original sample-size justification, planned power, interim analyses, and full statistical analysis plan are also not reported. These omissions limit the ability to assess how closely the posted analyses follow the trial’s intended analysis strategy. They do not negate the reported estimates, but they constrain evaluation of robustness, multiplicity, and the possible effect of missing observations.

The primary and secondary results also use different forms of outcome: a continuous mean change for the primary endpoint and binary response proportions for the ACR outcomes. Each has its own assumptions and uncertainty. A coherent interpretation considers the endpoint definitions and analysis methods together, rather than relying on a single p-value across outcomes.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: juvenile idiopathic arthritis (4.3%), abdominal pain upper (3.2%), headache (3.2%), cardiac failure congestive (2.2%), pain (2.2%).

During the double-blind comparison, the registry lists serious adverse events in 0 of 15 participants in the placebo group and 1 of 31 in the adalimumab group. These are event counts over the reported groups, not estimates of comparative safety with a precision claim. The record also reports other adverse events in 8 of 15 placebo participants and 21 of 31 adalimumab participants during that comparison.

The separate Any Adalimumab category lists 10 serious adverse events among 46 participants and other adverse events among 46 of 46. This is a distinct exposure grouping from the double-blind comparison and should not be directly contrasted with the randomized arms as if it represented the same follow-up or allocation. The record does not provide enough detail to reconstruct exposure duration for these aggregate safety counts.

Listed serious-event terms include JUVENILE IDIOPATHIC ARTHRITIS (4.3%), ABDOMINAL PAIN UPPER (3.2%), HEADACHE (3.2%), CARDIAC FAILURE CONGESTIVE (2.2%), PAIN (2.2%), and APPENDICITIS (2.2%). These terms are registry listings and do not by themselves establish causation. Death counts are not reported in the registry record.

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

The posted primary data describe average change in active-joint count over the specified period in the randomized double-blind comparison. The sponsor-reported ANCOVA estimate is a difference in final values with a confidence interval on the negative side of zero; the unadjusted recalculation differs and has a wider interval that includes zero. The discrepancy means the reported sponsor analysis should be the principal inferential result, while the recalculation is a separate descriptive check based on group summaries.

This statistical result does not describe the outcome of every participant. Group averages can conceal a range of individual changes, and a mean difference does not indicate how many participants improved, worsened, or remained unchanged. The secondary response outcomes provide a different view based on thresholds, but they are subject to uncertainty and multiple-comparison concerns.

The findings apply to the population, treatment schedule, comparator, endpoint definition, and follow-up reported for this trial. The primary comparison covers 12 weeks of double-blind treatment. Although the registry lists an open-label adalimumab period of up to 192 weeks, the information in the record does not establish a randomized placebo comparison across that duration. Long-term comparative conclusions should not be inferred from the short-term randomized outcome.

The record includes safety counts, but event counts alone do not determine whether an event was caused by study treatment, and the exposure groups differ across the listings. Neither these data nor the efficacy summaries justify medical advice or a claim about how a particular person should be treated. The results are best understood as estimates with method-specific uncertainty from one completed study, alongside reporting limitations in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why the analysis method is part of the result. The same primary endpoint has a sponsor-reported ANCOVA estimate and an unadjusted recalculation from arm summaries, and their confidence intervals lead to different inferential readings. Recognizing that distinction prevents a simple recalculation from being mistaken for the trial’s own analysis. Where the registry indicates a discrepancy, the sponsor’s reported analysis takes precedence.

It also demonstrates that an effect estimate and its precision should be considered together. The primary point estimates are substantial in magnitude on the reported percent-change scale, but the recalculated interval remains broad. Reporting only the point estimate or only a p-value would leave out important information about uncertainty. The standard deviations also show why variation among participants matters when comparing group means.

The secondary outcomes raise a further statistical issue: multiple endpoints can provide a broader clinical picture, but unadjusted tests across several outcomes should not be read as repeated independent confirmation. Missing-data handling matters too. LOCF is explicitly reported for the primary endpoint, but alternative sensitivity analyses are not reported in the registry record, limiting assessment of how robust the estimate is to that choice.

Finally, the planning illustrations show how the required number of participants depends on the effect size targeted and the desired power. They are not a record of the trial’s original design assumptions. Keeping design planning, observed data, and post hoc calculations separate is essential for sound interpretation.

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 randomized groups were small, and the primary endpoint showed substantial variability in the posted summaries. The resulting estimates should be read with their intervals rather than as exact values. The record identifies the ITT population and LOCF handling for the primary endpoint, but does not report the extent or pattern of missing data or sensitivity analyses using other assumptions.

The registry reports an ANCOVA result but does not provide the covariates or further model details needed to reproduce it. The unadjusted recalculation differs from the sponsor analysis, and the reason for that discrepancy is not reported in the registry record. This limits independent evaluation of the primary analysis. The registry record also does not report the original sample-size justification, a full statistical analysis plan, or interim-analysis details.

Multiplicity handling for the several secondary outcomes is not reported. Numerical results for some listed secondary joint outcomes are not reported in the registry record, limiting assessment of consistency across all outcome domains. The response outcomes are based on thresholds and therefore convey different information from the continuous primary endpoint.

The safety results include a randomized double-blind comparison and a separate Any Adalimumab category. Those groupings should not be treated as directly comparable without additional exposure and follow-up details. The record’s safety counts do not establish whether reported events were caused by treatment. The primary randomized endpoint is at Week 12; the presence of a longer open-label period does not supply a randomized long-term comparison in the information reported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of the Efficacy and Safety of Adalimumab in Pediatric Subjects With Enthesitis Related Arthritis — NCT01166282.
• Registry record last updated 2021-07-12; status last verified 2021-07.
• Results first posted 2016-06-21.
• 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

NCT01166282 is a completed randomized, quadruple-masked, parallel-group phase 3 study of adalimumab versus placebo in pediatric subjects with Enthesitis Related Arthritis. Enrollment was 46. The double-blind regimens were given every other week for 12 weeks, and the primary endpoint was percent change in active-joint count from baseline to Week 12 in the ITT population, with LOCF used for missing data.

The registry reports an ANCOVA primary analysis and additional secondary response and safety results. An unadjusted recalculation differs from the sponsor analysis, so the sponsor’s own result takes precedence. The original design assumptions, multiplicity strategy, and several analysis details are not reported in the registry record.