A Multi-center, Randomized, Double-blind, Placebo-controlled Study to Evaluate the Efficacy and Safety of Certolizumab Pegol in Combination With Methotrexate in the Treatment of Disease Modifying Antirheumatic Drugs (DMARD)-naïve Adults With Early Active Rheumatoid Arthritis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Multi-center, Randomized, Double-blind, Placebo-controlled Study to Evaluate the Efficacy and Safety of Certolizumab Pegol in Combination With Methotrexate in the Treatment of Disease Modifying Antirheumatic Drugs (DMARD)-naïve Adults With Early Active Rheumatoid Arthritis (NCT01519791), a randomized phase 3 study. The primary outcome is Percentage of Subjects in Sustained Remission at Week 52.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, double-blind, parallel-group, placebo-controlled study sponsored by UCB Pharma SA. It evaluated certolizumab pegol in combination with methotrexate for inducing and sustaining clinical response in DMARD-naïve adults with early active rheumatoid arthritis. The registry lists rheumatoid arthritis as the condition and enrollment of 880.

The registry record lists the study start as 2012-01 and primary completion as 2014-07, with status marked COMPLETED. The treatment arms represented in the posted results were certolizumab pegol plus methotrexate and placebo plus methotrexate. Arm-description text giving further details of the treatment schedules is not reported in the registry record. Details such as dosing, treatment duration, allocation ratio, and any stratification factors are also not reported in the registry record.

The primary outcome was the percentage of subjects in sustained remission at Week 52. The posted primary outcome analysis included 213 participants in the placebo plus methotrexate arm and 655 in the certolizumab pegol plus methotrexate arm. These are the outcome-analysis populations, not a restatement of the overall enrollment. The primary population was the Full Analysis Set Period 1, with Non-Responder Imputation for missing assessments.

The registry lists 30 outcome measures, five analyses, and 29 posted secondary outcomes. The secondary measures include sustained low disease activity, radiographic changes, radiographic non-progression, and ACR response outcomes. Details of the original sample-size justification, planned interim analyses, and full statistical 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.

Before assignment: A total of 880 subjects were randomized. Three subjects were randomized in error, were not dosed, and withdrawn shortly afterwards as screen failures. Two of them were included in the Randomized Set 1 (RS1) only and one of these three subjects was conservatively excluded from any output. Therefore, 879 subjects are in RS1.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set Period 1 (FAS1) with Non-Responder Imputation (NRI). FAS1 consisted of all subjects with valid Baseline and valid post-Baseline efficacy measurement within Period 1 for DAS28(ESR). For NRI, a subject having missing data for the time point assessed was conservatively counted as a nonremitter or nonresponder.

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: Baseline Charactersitics refer to the Randomized Set (RS).

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Subjects in Sustained Remission at Week 52, measured over Week 52.

The primary endpoint is the percentage of subjects in sustained remission at Week 52. Remission required DAS28(ESR) < 2.6 at both Weeks 40 and 52, so the endpoint reflects meeting the threshold at two assessments rather than at a single visit. The registry describes DAS28(ESR) as a score based on tender and swollen joint counts, erythrocyte sedimentation rate, and the patient’s global assessment of disease activity. Lower scores indicate less disease activity.

This is a binary outcome: each participant either meets the endpoint definition or does not. The posted results therefore report proportions in each treatment arm, rather than average changes in the underlying DAS28(ESR) score. For missing assessments, the primary analysis used Non-Responder Imputation, counting a participant with missing data at the assessed time point as a non-responder. This rule makes the endpoint definition and the handling of missing measurements part of the interpretation.

General statistical context: requiring the remission criterion at both visits is a way to operationalize sustained status over time. It does not describe every possible pattern of disease activity during the study, and it does not by itself explain the clinical importance of a particular difference in proportions. The registry record does not report a threshold for a clinically important between-arm difference.

7. Results Posted in the Registry

• Certolizumab Pegol + Methotrexate (Full Analysis Set): 28.9% (189/655) versus 15.0% (32/213) on control; risk difference 13.8 percentage points (95% CI 7.9 to 19.8), risk ratio 1.92 (1.37–2.70); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Subjects in Sustained Low Disease Activity (LDA) at Week 52

• 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:
  • Certolizumab Pegol + Methotrexate (Full Analysis Set): 43.8% (287/655) versus 28.6% (61/213) on control; risk difference 15.2 percentage points (95% CI 8.0 to 22.3), risk ratio 1.53 (1.22–1.92); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Certolizumab Pegol + Methotrexate (Full Analysis Set) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Modified Total Sharp Score (mTSS) to Week 52

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Certolizumab Pegol + Methotrexate (Radiographic Set): mean 0.20 versus 1.80 on control; difference -1.60 (95% CI -2.31 to -0.89), standardized effect d = -0.46; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Certolizumab Pegol + Methotrexate (Radiographic Set) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Subjects With Radiographic Non-progression From Baseline to Week 52

• 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:
  • Certolizumab Pegol + Methotrexate (Radiographic Set): 70.3% (371/528) versus 49.7% (81/163) on control; risk difference 20.6 percentage points (95% CI 12.0 to 29.2), risk ratio 1.41 (1.20–1.67); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Certolizumab Pegol + Methotrexate (Radiographic Set) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover more than one aspect of rheumatoid arthritis: sustained low disease activity, radiographic progression and structural scores, and ACR response criteria. The outcomes reported in the registry generally show higher percentages meeting favorable binary criteria in the certolizumab pegol plus methotrexate arm, and lower mean change in mTSS than in the placebo plus methotrexate arm. These endpoint families complement the primary sustained-remission result by describing other clinical and radiographic measures rather than repeating the same definition.

Secondary endpoints can help show whether the pattern of results extends beyond the primary outcome, but they do not carry the same evidential weight as a prespecified primary endpoint. The registry lists 29 posted secondary outcomes and 30 outcome measures overall. The multiplicity approach for these outcomes is not reported in the registry record. The unadjusted recalculated p-values therefore should be read cautiously: when many outcomes are examined, small p-values can arise by chance, and the strength of evidence depends in part on the planned testing strategy.

The secondary measures also use different outcome scales and analysis populations. For example, the mTSS change and radiographic non-progression results use a Radiographic Set, while the primary outcome uses a Full Analysis Set Period 1 with Non-Responder Imputation. Their sample sizes and missing-data considerations are therefore not identical. The registry’s posted analyses for some outcomes use different methods, including a rank-based analysis for mTSS. Such differences mean that the secondary outcomes should not be collapsed into one overall numerical summary.

One posted secondary outcome, radiographic non-progression, has no sponsor-reported analysis listed in the record, although arm-level results and a recalculated comparison are available. The absence of a reported analysis does not establish why it is absent. Overall, the secondary results add context to the primary endpoint but should be interpreted as a broader, multiplicity-sensitive set of observations rather than as independent confirmations of the primary finding.

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

• Percentage of Subjects in Sustained Low Disease Activity (LDA) at Week 52
• Change From Baseline in Modified Total Sharp Score (mTSS) to Week 52
• Percentage of Subjects With Radiographic Non-progression From Baseline to Week 52
• Change From Baseline in the Joint Erosion Score to Week 52
• Change From Baseline in the Joint Narrowing Score to Week 52
• Percentage of Subjects Meeting the American College of Rheumatology 20 % Response Criteria (ACR20) at Week 52
• Percentage of Subjects Meeting the American College of Rheumatology 50 % Response Criteria (ACR50) at Week 52
• Percentage of Subjects Meeting the American College of Rheumatology 70 % Response Criteria (ACR70) at Week 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary, because each participant is classified as having or not having sustained remission under the specified DAS28(ESR) criterion. The arm-level proportions give the share classified as meeting the endpoint in each group. The risk difference is an absolute comparison of those proportions. A value above zero in the direction used for the posted comparison corresponds to a higher proportion in the certolizumab pegol plus methotrexate group. The recalculated risk difference is 0.138, and its 95% confidence interval is 0.079 to 0.198.

General statistical context: a confidence interval describes a range of values reasonably compatible with the data under the method’s assumptions. It communicates uncertainty about an estimate; it is not a range containing a fixed proportion of individual participant outcomes. For a risk difference, zero is the no-difference reference. The interval reported for the recalculated comparison lies above that reference. The p-value, reported as p < 0.001, describes how incompatible the observed data are with a specified null model, assuming the model and analysis conditions hold. It does not measure the probability that the null hypothesis is true.

The registry’s reported primary analysis was logistic regression, with an odds ratio of 2.283 and a 95% confidence interval from 1.503 to 3.468. General statistical context: logistic regression models the log odds of a binary outcome. An odds ratio compares the odds between groups, whereas the risk difference compares proportions directly. An odds ratio is not a risk difference, and it does not directly state how many additional participants met the endpoint. The registry record does not describe the regression covariates, so it is not possible to determine from the posted analysis description which variables, if any, were included beyond the treatment-group comparison.

The unadjusted recalculation uses the posted arm-level summary results. It is not a substitute for the sponsor’s own model-based analysis. The reported analysis and recalculation are broadly aligned in direction, but they express the contrast using different statistical measures. The registry’s reported odds ratio and its confidence interval are the sponsor’s own analysis values; the recalculated risk difference and its interval are a simple unadjusted comparison derived from the posted summaries.

For this endpoint, the Full Analysis Set Period 1 included participants with valid baseline and post-baseline efficacy measurements within Period 1 for DAS28(ESR). The primary endpoint used Non-Responder Imputation. The registry states that a participant missing data for the time point assessed was conservatively counted as a non-responder. This approach prevents missing endpoint data from being counted as success, but it does not eliminate the possibility that missingness affects interpretation. The reasons for missing data and the extent of missingness by arm are not reported in the registry record.

The registry reports other statistical methods for secondary outcomes. The mTSS analysis used ANCOVA on ranks, with the reported parameter described as a Hodges-Lehmann point estimate of shift. General statistical context: rank-based approaches use the ordering of observations and can be useful when a conventional mean-based model may not fit the data well. The posted arm means and standard deviations are descriptive summaries, while the sponsor’s reported rank-based estimate answers a different model-based question. The registry record does not give further detail on the exact implementation of that analysis.

General statistical context: when count or continuous data show more variation than a simple model expects, over-dispersion can make standard errors too small if it is ignored. That general issue is not identified as a specific feature of the primary binary endpoint in the registry record. The primary outcome is reported as proportions and analyzed with logistic regression; the exact model diagnostics and assumptions are not reported in the registry record.

The endpoint definition also matters statistically. Sustained remission requires the threshold to be met at both Weeks 40 and 52. That differs from an endpoint based on status at only one visit or a change in the continuous DAS28(ESR) score. A participant with a missing value at the assessed time point was counted as a non-responder under the stated imputation rule. The registry record does not report additional sensitivity analyses for alternative missing-data assumptions.

Finally, the posted p-values for the recalculated binary comparisons are unadjusted. General statistical context: when many outcomes are examined, the chance of observing at least one small p-value by chance can increase. Whether and how to account for multiple comparisons depends on the prespecified testing strategy. The multiplicity strategy for the full set of outcomes is not reported in the registry record, so the secondary p-values should not be treated as if a particular correction or hierarchical testing procedure had been documented.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.138, with a 95% confidence interval from 0.079 to 0.198. The interval lies above zero, the no-difference reference for a risk difference. It describes uncertainty around the estimated absolute contrast in the proportions meeting the endpoint. It does not mean that the true value is known exactly, and it does not account for every possible source of uncertainty, such as limitations in the endpoint definition or missing-data assumptions.

The registry’s reported logistic-regression odds ratio is 2.283, with a 95% confidence interval from 1.503 to 3.468. For an odds ratio, one is the no-association reference. The interval lies above that value. The odds ratio interval should be interpreted on the odds scale, not as a confidence interval for a difference in percentages. The recalculated risk-difference interval and the sponsor’s odds-ratio interval therefore cannot be compared by their numerical widths alone.

General statistical context: a confidence interval reflects sampling uncertainty under the analysis method and its assumptions. A narrower interval indicates greater precision on the scale being estimated, while a wider interval indicates more uncertainty. Precision is not the same as clinical importance, and an interval alone does not determine whether the observed contrast matters to patients. The registry record does not report a threshold for a clinically meaningful difference in sustained remission.

The primary outcome analysis included 213 participants in the placebo plus methotrexate group and 655 in the certolizumab pegol plus methotrexate group. The unequal group counts are relevant context when reading the estimates, but the confidence intervals are the direct summary of statistical precision for each reported effect. The registry does not report confidence intervals for the arm-level percentages themselves in the posted primary outcome results. The interval for the recalculated risk difference is based on an unadjusted comparison and should be distinguished from the reported regression interval.

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 for 80% power and participants per arm for 90% power. They are not total-event counts. The planning illustration uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It considers effects equal to 100%, 75%, or 50% of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

In plain terms, the 80% power column gives the estimated participants needed in each arm for an 80% chance of detecting the specified effect under the planning assumptions, if that effect is the true one and the assumptions hold. The 90% column gives the corresponding number for a 90% chance. These are planning illustrations, not guarantees about what a future study will find. They are calculated from the observed effect rather than from the trial’s original design assumptions; this is not observed power.

For the primary binary outcome, the illustration ranges from 140 participants per arm for planning based on 100% of the observed effect to 494 per arm for planning based on 50% of the observed effect at 80% power. At 90% power, the corresponding figures are 187 and 660 participants per arm. Planning for 75% of the observed effect requires 235 participants per arm for 80% power and 313 for 90% power.

The same pattern applies across the other outcomes: smaller effects require more participants to detect under the stated assumptions. These figures should not be interpreted as a reconstruction of the actual trial design, nor as evidence that the completed trial had a particular probability of success.

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 = 0.150; treatment proportion p₁ = 0.289; average p̄ = 0.219.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5853 = 1.1471.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5770 = 0.4856.
4. n = (1.1471 + 0.4856)² / (0.1383)² = 139.3, rounded up to 140 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 <- 0.150234741784038                          # control proportion
p1 <- 0.288549618320611                          # 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(1519791)
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 = 140 (80% power), 187 (90% power)
 75% of observed effect: n per arm = 235 (80% power), 313 (90% power)
 50% of observed effect: n per arm = 494 (80% power), 660 (90% power)
power.prop.test: 139.3 
Simulated power at n = 140 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 the sponsor’s primary analysis as logistic regression, with an odds ratio of 2.283, a 95% confidence interval from 1.503 to 3.468, and p < 0.001. The unadjusted recalculation from the posted arm summaries estimates a risk difference of 0.138, with a 95% confidence interval from 0.079 to 0.198 and p < 0.001. Both comparisons point in the same direction, but they use different effect measures and should not be treated as numerically interchangeable.

The odds ratio compares odds, while the risk difference compares proportions. The registry’s regression result may reflect a model-based analysis, but the covariates and detailed model specification are not reported in the registry record. The recalculation is explicitly unadjusted and uses the posted summary statistics. It is useful as a transparent comparison of the arm-level outcome proportions, but it does not replace the sponsor’s own analysis.

The registry record does not flag a discrepancy between the recalculated and reported analysis. The reported analysis therefore remains the primary account of the sponsor’s model-based result, while the recalculation provides a complementary absolute-scale estimate. Neither measure alone settles the clinical meaning of the observed contrast.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 30 outcome measures, five analyses, and 29 posted secondary outcomes. This is a broad collection of endpoints, covering clinical status, radiographic measures, and response criteria. The registry record does not report a multiplicity adjustment, a hierarchy for testing outcomes, or a prespecified strategy controlling the overall type I error across the full outcome set. The unadjusted p-values for secondary outcomes should therefore be treated as exploratory evidence rather than as though the record established a formal family-wise testing plan.

The primary endpoint is clearly identified as the percentage of subjects in sustained remission at Week 52. The reported sponsor analysis uses logistic regression, but detailed model terms and covariate adjustments are not reported in the registry record. The registry also does not report interim analyses or the original sample-size justification. These omissions limit assessment of how the statistical plan was set before the results were known, but they do not change the numerical results posted for the endpoint.

The primary analysis population is the Full Analysis Set Period 1. It included participants with valid baseline and post-baseline efficacy measurements within Period 1 for DAS28(ESR). For Non-Responder Imputation, a participant missing data for the assessed time point was counted as a non-responder. This is a conservative rule in the sense that missing status is not counted as meeting remission, but its effect depends on how much data are missing and why they are missing. The extent and reasons for missing primary outcome data by arm are not reported in the registry record.

The record does not report sensitivity analyses testing alternative assumptions about missing outcomes, nor does it describe whether other analysis populations were used for the primary endpoint. It also does not give the full set of participant flow details needed to trace exclusions from enrollment into each analysis population. These gaps make it harder to assess how robust the endpoint estimate is to changes in analytic assumptions. They should be distinguished from the stated NRI approach, which is explicitly described for the primary endpoint.

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: pneumonia (1.4%), latent tuberculosis (0.9%), pneumonitis (0.9%), pulmonary embolism (0.9%), osteoarthritis (0.6%).

The registry reports serious adverse events affecting 20 of 217 participants in the placebo plus methotrexate group and 70 of 659 participants in the certolizumab pegol plus methotrexate group. Other adverse events are reported for 63 of 217 participants and 248 of 659 participants, respectively. These figures use safety populations that differ from the primary outcome analysis counts. They are counts of participants with events against the stated at-risk populations, not a comparison adjusted for follow-up time or other factors.

The listed serious adverse event terms include pneumonia at 1.4%, latent tuberculosis at 0.9%, pneumonitis at 0.9%, pulmonary embolism at 0.9%, osteoarthritis at 0.6%, and atrial fibrillation at 0.5%. The registry record does not provide further detail in these figures about event severity beyond the serious-event classification, timing, recurrence, or causal relationship to treatment. Death counts are not reported in the registry record.

These safety counts provide descriptive context, not a complete safety assessment. Differences in the group counts should not be interpreted as a treatment effect without accounting for exposure, event definitions, follow-up, and the study’s safety analysis methods. Those details are not reported in the registry record.

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

The posted primary result describes the proportion of participants who met a specific sustained-remission definition: DAS28(ESR) < 2.6 at both Weeks 40 and 52. That proportion was 15.0% in the placebo plus methotrexate group and 28.9% in the certolizumab pegol plus methotrexate group. The result supports a statistical contrast between these observed trial groups under the endpoint definition and analysis approach reported in the registry.

It does not mean that every participant in either group experienced the same course, or that the group-level difference predicts an individual participant’s outcome. Nor does it establish what would happen under different treatment schedules, in different populations, or beyond the trial’s follow-up. The registry describes a randomized, double-blind study, but does not report details such as the treatment schedules or the full analysis plan. The registry also does not report a threshold for a clinically important difference in sustained remission.

The primary analysis used Non-Responder Imputation, counting missing endpoint assessments as failures to meet the endpoint. The result is therefore conditional on that missing-data rule as well as on the observed measurements. The amount and reasons for missingness are not reported in the registry record, so the sensitivity of the estimate to alternative assumptions cannot be assessed from the posted information.

The p-value indicates statistical compatibility with a no-difference model, not the probability that the treatment has a particular effect. The confidence interval communicates uncertainty around the estimated contrast but does not capture every limitation in the outcome definition, analysis population, or reporting. Secondary outcomes offer additional perspectives, but their number and unreported multiplicity strategy mean that they should not be treated as separate, definitive confirmations.

These results are statistical descriptions of the posted trial data. They are not medical advice and do not replace an assessment of the full study record, broader evidence, or individual circumstances.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares two treatment strategies under a randomized, double-blind, placebo-controlled design and defines its primary outcome in a reproducible way. The endpoint requires remission status at both Weeks 40 and 52, making the target outcome sustained remission rather than a single-visit threshold. That definition makes clear what the primary proportions represent and what they do not represent.

The primary result can be expressed on two scales. The registry reports an odds ratio from logistic regression, while the unadjusted recalculation expresses the arm contrast as a risk difference. The distinction matters: the odds scale is common in regression models, while an absolute difference in proportions can be easier to connect to the observed group outcomes. Reading both helps prevent an odds ratio from being mistaken for a percentage-point change.

The analysis also illustrates why missing-data rules matter. The primary outcome used Non-Responder Imputation, counting missing assessments as non-responses. That makes the classification rule explicit, while the unreported extent and reasons for missingness remain important limits on interpretation. The sample-size illustrations show how the number of participants needed for planning depends on the assumed effect size and desired power, without claiming to reconstruct the actual trial design.

Finally, the trial reports a broad range of secondary clinical and radiographic measures. Their breadth can help contextualize the primary result, but also raises the importance of a clearly reported multiplicity strategy. The record’s reporting gaps make these distinctions useful for statistical readers: a result’s meaning depends not only on its point estimate and p-value, but also on the endpoint, analysis population, model, missing-data handling, and scope of the conclusions.

19. Limitations

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

Several trial-specific reporting gaps constrain interpretation. The registry record does not report the original sample-size justification, the study’s detailed statistical analysis plan, or whether interim analyses were conducted. It does not provide treatment schedules in the arm descriptions, the allocation ratio, or the detailed covariates used in the logistic regression. These omissions prevent a full assessment of how the analyses were planned and implemented.

The primary analysis population is described, but the record does not give the extent or reasons for missing primary outcome data by arm. The NRI rule is stated, yet the record does not report sensitivity analyses under alternative missing-data assumptions. Additional participant flow details sufficient to trace enrollment into every outcome-specific population are also not reported in the registry record.

The registry lists many outcomes, but the strategy for handling multiplicity is not reported. Secondary p-values therefore require caution, especially where sponsor-reported analyses are absent. The posted arm counts and outcome summaries also differ by analysis population: the primary endpoint uses the Full Analysis Set Period 1, while radiographic outcomes use the Radiographic Set. Those populations should not be treated as interchangeable.

The safety record gives participant counts for serious and other adverse events, but the details needed to interpret exposure-adjusted risk, timing, causality, and event recurrence are not reported in the registry record. Death counts are not reported in the registry record. These limitations do not invalidate the posted results, but they define what can be concluded from the registry information alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Multi-center, Randomized, Double-blind, Placebo-controlled Study to Evaluate the Efficacy and Safety of Certolizumab Pegol in Combination With Methotrexate in the Treatment of Disease Modifying Antirheumatic Drugs (DMARD)-naïve Adults With Early Active Rheumatoid Arthritis — NCT01519791.
• Registry record last updated 2026-08-25; status last verified 2026-08.
• Results first posted 2015-09-22.
• 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

NCT01519791 is a completed Phase 3, randomized, double-blind, parallel-group, placebo-controlled study sponsored by UCB Pharma SA. It enrolled 880 DMARD-naïve adults with early active rheumatoid arthritis and compared certolizumab pegol plus methotrexate with placebo plus methotrexate. The registry lists the study start as 2012-01 and primary completion as 2014-07.

The primary endpoint was sustained remission at Week 52, defined as DAS28(ESR) < 2.6 at both Weeks 40 and 52. The posted proportions were 15.0% and 28.9%, respectively. The registry reports a logistic-regression odds ratio of 2.283, with a 95% confidence interval from 1.503 to 3.468 and p < 0.001. The primary population used Non-Responder Imputation. The record also lists a broad set of secondary clinical and radiographic outcomes, while important details of the original statistical plan and multiplicity strategy are not reported in the registry record.