Golimumab in Rheumatoid Arthritis Participants With an Inadequate Response to Etanercept (ENBREL) or Adalimumab (HUMIRA): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Golimumab in Rheumatoid Arthritis Participants With an Inadequate Response to Etanercept (ENBREL) or Adalimumab (HUMIRA) (NCT01004432), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving Erythrocyte Sedimentation Rate (ESR)-Based American College of Rheumatology [ACR] 20 Response at Week 14.

2. Clinical Question

The clinical question concerns switching treatment in participants whose rheumatoid arthritis was inadequately controlled on one of two existing treatment combinations. The initial study phase assessed subcutaneous golimumab with methotrexate. A later randomization applied only to participants who did not achieve a DAS28 good response at Week 16, while those who achieved that response continued subcutaneous golimumab. The registry describes an open-label overall group as well as double-blind groups and an open-label extension.

This staged design means that the primary Week 14 endpoint and the later Week 16 treatment assignment address different points in the study. The primary endpoint was measured before the described Week 16 randomization. The record does not report a Week 14 comparison against continued etanercept, adalimumab, or placebo. It therefore does not provide a randomized estimate of the effect of switching from the original treatments at the primary endpoint.

The registry record identifies the study as randomized, quadruple-masked, and crossover, but its arm descriptions also distinguish open-label and double-blind periods and response-based treatment paths. The precise interpretation of the design label should be considered alongside those descriptions. The registry does not report enough detail to reconstruct every treatment sequence or the analysis used for the primary endpoint.

3. Trial Design

The study was a Phase 3b multicenter investigation of golimumab in rheumatoid arthritis participants with inadequate disease control despite treatment with etanercept or adalimumab. The registry lists randomized allocation, quadruple masking, and a crossover model. It records enrollment of 433 participants, a start date of 2009-12, primary completion in 2013-07, and completed status.

All enrolled and dosed participants in the open-label overall group received golimumab 50 mg subcutaneously every 4 weeks with methotrexate from Week 0 to Week 12. At Week 16, treatment paths were described according to DAS28 response. Participants who achieved a DAS28 good response received golimumab 50 mg subcutaneously every 4 weeks with methotrexate through Week 48. Participants who did not achieve a good response were randomly assigned to one of two double-blind groups: continued subcutaneous golimumab with placebo intravenous infusions, or intravenous golimumab with placebo subcutaneous injections, both with methotrexate.

The record describes intravenous golimumab at 2 mg/kg and placebo-matched subcutaneous injections in one double-blind group. The other double-blind group continued subcutaneous golimumab and received placebo-matched intravenous infusions. The listed administration schedule for the intravenous group includes infusions at Week 16, 20, 28, 36, and 44. The description of the other group lists infusions at Week 16, 20, 28, but is incomplete in the registry record. Participants completing the main study who met the extension criteria could receive subcutaneous golimumab with methotrexate from Week 52 to Week 72.

The study’s sequential treatment paths matter when interpreting comparisons. The Week 14 primary endpoint occurred before the response-based Week 16 assignment described in the record. The registry does not report a primary endpoint comparison between two randomized arms. It also does not report the protocol details needed to reconcile fully the crossover label with the open-label and response-based arm descriptions.

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.

Open-label (OL) Period (Week 0 - 16)

Reasons for not completing this period:

OL/Double-Blind (DB) Period (Week 16-52)

Reasons for not completing this period:

OL Study Extension (Week 52 - 76)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified Intent To Treat (mITT) population included all enrolled participants who had Week 0 measurements and received at least 1 dose of study drug.

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 Achieving Erythrocyte Sedimentation Rate (ESR)-Based American College of Rheumatology [ACR] 20 Response at Week 14, measured over Week 14.

The primary endpoint is the percentage of participants achieving an erythrocyte sedimentation rate (ESR)-based American College of Rheumatology 20 response at Week 14. The endpoint is binary at the participant level: a participant either meets the response definition or does not. The registry specifies the modified Intent To Treat population, consisting of enrolled participants who had Week 0 measurements and received at least one dose of study drug.

To qualify as a responder, a participant needed at least 20% improvement from baseline in both tender-joint and swollen-joint counts. The definition also required at least 20% improvement from baseline in three of five assessments: participant-rated pain, participant global disease activity, physician global disease activity, physical function measured by the Health Assessment Questionnaire Disability Index, and ESR. The joint counts involved 68 tender joints and 66 swollen joints; the assessment scales and score ranges are described in the registry record.

ACR20 is a composite response measure. Requiring improvement across joint counts and several other domains makes the endpoint broader than a change in a single symptom or laboratory measure. ESR-based means ESR is one of the assessments that can contribute to the required set of improvements; the definition does not require improvement in all five additional assessments.

The registry lists a 95% confidence interval as the endpoint’s dispersion measure, but the primary response estimate and its interval are not reported in the registry record. Without those values, the magnitude and precision of the Week 14 response cannot be assessed from the posted results.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a binary percentage: participants are classified as responders or nonresponders according to the ACR20 definition. For a binary outcome, the response percentage describes the fraction of participants meeting the endpoint within the analyzed group. A comparative analysis would ordinarily also specify a contrast between groups, such as a difference in response proportions, with uncertainty around that contrast. The registry does not report a primary response estimate or a two-arm primary comparison.

What does the confidence interval contribute?

In general, a confidence interval communicates uncertainty around an estimate. It is not a guarantee that a particular range contains the true value, and it does not replace an estimate of the effect itself. The primary endpoint lists a 95% confidence interval as its dispersion measure, but neither the response percentage nor its interval is reported in the registry record. It is therefore not possible to discuss the observed precision of the primary endpoint.

The definition requires improvement in joint counts and a minimum number of additional assessments. This composite structure can capture response across several aspects of rheumatoid arthritis, but it also means the classification depends on multiple measurements and thresholds. In general, a participant near a response threshold may be classified differently from one just beyond it even when their underlying health changes are similar. The registry’s endpoint definition specifies the threshold but does not report individual-level data or sensitivity analyses around that definition.

How should the design be understood?

The record labels the study randomized, quadruple-masked, and crossover, while the arm descriptions detail open-label treatment followed by response-based treatment paths, including random assignment among participants who did not achieve a DAS28 good response at Week 16. The primary endpoint is assessed at Week 14. These registry entries indicate that the Week 14 outcome precedes the later randomization described in the arm details. The registry does not report a randomized two-arm analysis for the primary endpoint, and it does not report enough protocol or analysis detail to explain fully how the crossover label relates to the treatment sequence.

Randomization is generally used to make assigned treatment groups comparable at baseline, on average, for both measured and unmeasured characteristics. Masking is generally intended to reduce the influence of knowledge of treatment assignment on participant experience, clinical assessment, or study conduct. Those general principles do not establish that a particular analysis was unbiased; details about implementation and analysis are necessary. The registry lists allocation and masking categories but does not report further details about the procedures.

Response-dependent assignment later in the study creates a selected population for those randomized comparisons. In general, results among people selected because they did not meet a response criterion answer a question about that selected group, not necessarily about all enrolled participants. The later treatment paths also differ from the primary Week 14 endpoint in timing and eligibility. The registry’s posted primary outcome does not provide the analysis needed to quantify a contrast for either stage.

What do the sample-size illustrations mean?

Sample-size calculations in general estimate how many participants might be needed to detect a specified effect under stated assumptions. They are planning illustrations, not observed power and not evidence that the original trial was designed around those assumptions. The calculation assumptions described for the illustrations include a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and effects defined as fractions of the observed effect. The registry does not report the trial’s own sample-size justification, so the illustrations should not be read as its original design target or as a retrospective measure of success.

For non-time-to-event outcomes, the illustration convention is participants per arm; time-to-event illustrations use a total event count. These are general planning conventions and do not change the status of the posted outcomes. The primary result is still not reported as a two-arm comparison, and no sample-size illustration can fill in a missing response estimate or confidence interval.

Why can over-dispersion matter?

For a binary outcome, a simple model may assume that observations are independent and that variability follows the model’s expected structure. In general, over-dispersion means the observed variability exceeds that expectation. If relevant, failing to account for it can make uncertainty estimates too small. The registry record does not report an over-dispersion assessment or identify a model for the primary outcome, so no claim can be made about whether this issue applied or how it was handled.

The same caution applies to missing observations, covariate adjustment, and analysis populations beyond the definition of the modified Intent To Treat population. These are important statistical choices, but the registry record does not report the primary analysis method or enough detail to reconstruct it. The posted endpoint definition alone is not a substitute for a statistical analysis plan.

10. Exact Estimates for Each Arm

No two-arm comparison is shown for this trial, but each arm's result can still be summarized with exact interval estimates computed from the posted counts. The Clopper-Pearson interval is exact and conservative; the Wilson interval is a common closer-to-nominal alternative; the Bayesian credible interval uses a uniform Beta(1, 1) prior. For small groups the three can differ noticeably.

R code and output

arm    <- c("OL Overall Group: Golimumab 50 mg SC + MTX")
n      <- c(433)
events <- c(151)
for (i in seq_along(n)) {
  ci <- binom.test(events[i], n[i])$conf.int          # Clopper-Pearson exact interval
  cr <- qbeta(c(0.025, 0.975), 1 + events[i], 1 + n[i] - events[i])   # Bayesian, uniform Beta(1,1) prior
  wi <- (function(x, n) { p <- x / n; z <- qnorm(0.975); d <- 1 + z^2 / n
    c((p + z^2 / (2 * n) - z * sqrt(p * (1 - p) / n + z^2 / (4 * n^2))) / d, (p + z^2 / (2 * n) + z * sqrt(p * (1 - p) / n + z^2 / (4 * n^2))) / d) })(events[i], n[i])
  cat(sprintf("ARM|%s|%d|%d|%.1f|%.1f|%.1f|%.1f|%.1f|%.1f|%.1f\n", arm[i], n[i], events[i], 100 * events[i] / n[i],
              100 * ci[1], 100 * ci[2], 100 * wi[1], 100 * wi[2], 100 * cr[1], 100 * cr[2]))
}

ARM  OL Overall Group: Golimumab 50 mg SC + MTX  433  151  34.9  30.4  39.6  30.5  39.5  30.5  39.5

11. Multiplicity, Missing Data and Analysis Populations

The registry lists six outcome measures and one analysis, but does not report a multiplicity adjustment or testing hierarchy. Multiplicity arises in general when several outcomes, timepoints, or treatment comparisons are tested; without an appropriate plan, the chance of at least one apparently positive result can increase. The registry record does not report whether multiplicity was addressed in the trial’s statistical plan, so no adjustment method or confirmatory status should be inferred.

The primary endpoint is defined for the modified Intent To Treat population: enrolled participants with Week 0 measurements who received at least one dose of study drug. This definition excludes people who did not meet either condition. The registry does not report how missing Week 14 measurements were handled, whether participants with incomplete component assessments were classified as nonresponders, or whether any imputation or sensitivity analyses were conducted. Those details are not reported in the registry record.

In general, missing outcome data can affect an estimated response percentage when the likelihood of missingness is related to treatment assignment or outcome status. Different assumptions about missing outcomes can lead to different estimates. Without the missing-data rules and relevant counts, the extent or direction of any such influence cannot be assessed.

The registry describes a later response-based treatment assignment at Week 16, but does not report whether the primary analysis adjusted for baseline characteristics or other variables. It also does not report a statistical analysis plan or sample-size justification. The sample-size assumptions described for planning illustrations are not a substitute for the trial’s own rationale, and they do not reveal how the primary endpoint was analyzed.

12. 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: chest pain (1.6%), intentional overdose (1.3%), muscular weakness (1.3%), pain in extremity (1.3%), oesophagitis haemorrhagic (1.1%).

The registry reports serious adverse event counts and other adverse event counts for the listed groups, alongside the number at risk in each group. In the open-label overall group, serious adverse events affected 20 of 433 participants, and other adverse events affected 123 of 433. In the open-label Group 1, the corresponding counts were 2 of 75 and 21 of 75. In double-blind Group 2a, the counts were 4 of 91 and 30 of 91; in double-blind Group 2b, they were 10 of 184 and 54 of 184. In the open-label extension group, they were 10 of 212 and 61 of 212.

These are group-specific counts, not a single comparison across randomized groups. The listed groups represent different study periods and treatment paths, and the record does not establish that their participants or exposure periods are directly comparable. The overall group and later groups should not be added together to create a new total, because participants may appear in more than one study stage.

The registry lists several top serious adverse event terms with percentages, including chest pain at 1.6%, intentional overdose and muscular weakness at 1.3% each, pain in extremity at 1.3%, and oesophagitis haemorrhagic and pneumonia at 1.1% each. The record does not provide the denominator or further details for interpreting those term-specific percentages. Death counts are not reported in the registry record.

In general, event counts describe what was recorded during the specified study periods; they do not by themselves establish that treatment caused an event. Comparisons of safety require attention to exposure, follow-up, group formation, and event definitions, details that are not fully reported in the registry record.

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

The posted record establishes the study’s purpose, treatment sequence, primary endpoint definition, and some adverse event counts. It does not report a numerical result for the primary Week 14 response endpoint. Without the response estimate and its confidence interval, readers cannot assess the observed response frequency or how precisely it was estimated.

The primary outcome was skipped because there were fewer than two arms in the primary outcome. This is important because a clinical trial question about whether outcomes differ between treatments requires an interpretable comparison. A response rate within one group, even if it were reported, would not by itself show how that group compares with another treatment. The registry does not report a primary two-arm efficacy comparison.

The record’s Week 16 randomization concerns participants who did not achieve a DAS28 good response at that point. That later comparison, if reported, would apply to the selected group defined by its Week 16 response status; it would not automatically answer the primary Week 14 question or represent all enrolled participants. The registry does not report later efficacy estimates in the information described for the primary result.

The registry also does not report the trial’s full statistical analysis plan, handling of missing outcome data, or sample-size justification. These omissions limit assessment of analysis choices and the robustness of any effect estimate. Sample-size illustrations based on stated assumptions are planning exercises, not observed power and not substitutes for the trial’s own design rationale.

Safety counts can be described as counts among the participants at risk in each listed group, but they are not enough to establish comparative safety. The groups differ in treatment path and may overlap across stages. The record does not provide the details needed to interpret the counts as a direct treatment contrast.

Accordingly, the registry record supports a careful account of what was planned and which adverse events were recorded, but not a quantitative conclusion about the primary efficacy effect. This is a statement about what the posted record reports, not a claim that the study did or did not find a particular result elsewhere.

14. Why This Trial Matters Statistically

This study raises several statistical issues that are common in trials with staged treatment strategies. The initial treatment period, response-based treatment assignment, and extension period address distinct questions. Separating those stages helps avoid treating a result from a selected later group as though it described every participant enrolled at the start.

The primary endpoint is defined as a binary composite response at a specified time. Its interpretation depends on both the clinical threshold and the population in which it is evaluated. The registry describes the modified Intent To Treat population and the joint and other assessment criteria, allowing readers to understand the endpoint’s structure. However, the primary response estimate and interval are not reported, so its magnitude and precision remain unknown from this record.

The record also illustrates why design labels alone are not enough to interpret a study. It lists randomization, quadruple masking, and a crossover model, while the arm descriptions outline open-label treatment and later randomization based on response. Understanding which groups are comparable for a particular endpoint requires attention to when assignment occurred and who was eligible at that stage.

For statistical reporting, a treatment effect estimate with an uncertainty interval is central to judging the scale and precision of a comparison. A skipped primary comparison cannot be replaced by the enrollment number, by a safety count, or by a planning calculation. Sample-size illustrations can explain hypothetical planning under stated assumptions, but they do not establish what the trial was designed to detect or what it observed.

The study therefore matters statistically as an example of how endpoint timing, response-based selection, incomplete outcome reporting, and safety-group definitions shape interpretation. The registry’s information makes some design features and outcome definitions clear, while leaving the primary efficacy comparison unavailable. Recognizing that distinction is essential to avoid reading more into the record than it can support.

15. 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 principal limitation for interpreting efficacy is that the primary Week 14 response estimate and its 95% confidence interval are not reported in the registry record. The primary outcome is identified as skipped because there were fewer than two arms in the primary outcome. This prevents assessment of the primary response frequency, its precision, or a treatment contrast at that timepoint.

The registry identifies the study as randomized, quadruple-masked, and crossover, but the arm descriptions also distinguish open-label treatment, double-blind treatment, and response-based assignment at Week 16. The record does not report details sufficient to reconcile the design label with all treatment sequences or to determine how any crossover features were analyzed.

The primary endpoint was assessed at Week 14, before the later randomization described for participants who did not achieve a DAS28 good response at Week 16. The registry does not report a primary comparison against the original etanercept or adalimumab treatments, or a concurrent control group at Week 14. Therefore, the endpoint description does not establish a comparative treatment effect.

Information on missing-data handling, the statistical analysis plan, covariate adjustment, and the trial’s own sample-size rationale is not reported in the registry record. The record also does not provide sufficient detail to assess whether the later treatment groups had comparable follow-up or exposure for safety comparisons. The listed adverse event groups represent different stages and may include participants who continued through more than one stage, so their counts should not be treated as independent groups.

These limitations concern the available registry record. They do not establish what may have been reported in other materials, nor do they establish that a particular analysis was or was not conducted outside the record.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Golimumab in Rheumatoid Arthritis Participants With an Inadequate Response to Etanercept (ENBREL) or Adalimumab (HUMIRA) — NCT01004432.
• Registry record last updated 2015-04-30; status last verified 2015-04.
• Results first posted 2014-05-13.
• 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.

19. Record Summary

The registry record describes a completed Phase 3b multicenter study of golimumab in rheumatoid arthritis participants with inadequate disease control despite etanercept or adalimumab treatment with methotrexate. It lists enrollment of 433, randomized allocation, quadruple masking, and a crossover model. Initial treatment involved subcutaneous golimumab with methotrexate, followed by treatment paths that depended in part on Week 16 DAS28 response.

The primary endpoint was the percentage achieving an ESR-based ACR20 response at Week 14 in the modified Intent To Treat population. The response definition required improvement in tender and swollen joint counts and in at least three of five additional assessments. The primary estimate and confidence interval are not reported in the registry record, and the primary outcome is noted as skipped because fewer than two arms were available.

Serious and other adverse event counts are reported for the overall, response-based, double-blind, and extension groups. Those counts describe their respective groups and should not be treated as a direct comparative safety analysis. The registry does not report the primary statistical analysis plan, missing-data methods, or trial sample-size justification.