Dosing Flexibility Study in Patients With Rheumatoid Arthritis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dosing Flexibility Study in Patients With Rheumatoid Arthritis (NCT00580840), a randomized phase 4 study. The primary outcome is Percentage of ACR20 (American College of Rheumatology 20% Improvement) Responders at Week 34 in Patients Randomized at Week 18.

2. Clinical Question

3. Trial Design

The registry record describes a Phase 4, randomized, double-blind, parallel-group study in patients with active rheumatoid arthritis. Its official title also describes an open-label run-in followed by a double-blind, placebo-controlled randomized study. The overall enrollment was 333, and the trial status is completed. The record gives a start of 2007-12 and primary completion of 2010-12.

During the run-in, certolizumab pegol was administered at 400 mg at Weeks 0, 2, and 4, followed by 200 mg with placebo at Weeks 6, 8, 10, 12, 14, and 16. At Week 18, patients were grouped as responders or non-responders based on ACR20 results at Week 16. The record does not report the detailed rationale for this run-in or the subsequent treatment assignment process beyond describing the randomized study.

The primary analysis concerns patients randomized at Week 18, rather than everyone enrolled in the run-in. The full analysis set included 208 patients: 69 assigned to certolizumab pegol 400 mg and placebo plus methotrexate, 70 assigned to certolizumab pegol 200 mg and placebo plus methotrexate, and 69 assigned to placebo plus methotrexate. The primary outcome was assessed at Week 34. The record does not report why the analysis population was smaller than the total run-in enrollment.

The arm descriptions indicate different injection schedules for the two certolizumab regimens. The 400 mg regimen used certolizumab pegol every four weeks and placebo every four weeks, with injections alternating every two weeks. The 200 mg regimen used certolizumab pegol and placebo every two weeks, one injection of each. The placebo group received two placebo injections every two weeks. All groups are described in the primary endpoint as receiving methotrexate. Details such as the trial's original allocation concealment procedures and the exact procedures used to maintain masking 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.

Run-in

Reasons for not completing this period:

Double-Blind

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Of the 208 subjects in the Full Analysis Set (FAS) 208 subjects (69 400 mg CZP, 70 200 mg CZP, 69 placebo) are included in this analysis which uses Non-Response Imputation (NRI).

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 ACR20 (American College of Rheumatology 20% Improvement) Responders at Week 34 in Patients Randomized at Week 18, measured over Baseline, Week 34.

The primary endpoint is the percentage of patients randomized at Week 18 who were ACR20 responders at Week 34. ACR20 is a composite response definition: a patient must have at least 20% improvement from baseline in both tender joint count and swollen joint count, and improvement in at least three of five other core measures. Those additional measures cover physical function, inflammation, pain, and patient and physician assessments of disease activity.

A threshold-based endpoint turns several clinical measurements into a responder classification. It can make the outcome easier to interpret as the proportion of patients meeting a stated response standard, while retaining information from more than one aspect of disease assessment. It also discards detail: patients just below and just above the threshold are classified differently even if their underlying measurements are similar, and the endpoint does not convey the size of improvement among responders.

The primary analysis used non-responder imputation for missing values. Under this approach, missing outcome values are treated as non-response for the endpoint. This creates a clear rule for the binary outcome, but the resulting percentages depend in part on that missing-data assumption. The registry record does not report further sensitivity analyses for missing outcomes. The response percentages therefore should be read as results under the stated analysis rule, not as a complete description of every patient's observed disease measurements.

7. Results Posted in the Registry

• Certolizumab Pegol 200 mg and Placebo + Methotrexate: 67.1% (47/70) versus 65.2% (45/69) on control; risk difference 1.9 percentage points (95% CI -13.8 to 17.7), risk ratio 1.03 (0.81–1.31); unadjusted two-proportion z-test p = 0.810.
• Placebo + Methotrexate: 44.9% (31/69) versus 65.2% (45/69) on control; risk difference -20.3 percentage points (95% CI -36.5 to -4.0), risk ratio 0.69 (0.50–0.94); unadjusted two-proportion z-test p = 0.017.

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 ACR50 (American College of Rheumatology 50% Improvement) Responders at Week 34 in Patients Randomized at Week 18

• 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 200 mg and Placebo + Methotrexate: 50.0% (35/70) versus 52.2% (36/69) on control; risk difference -2.2 percentage points (95% CI -18.8 to 14.4), risk ratio 0.96 (0.69–1.33); unadjusted two-proportion z-test p = 0.798.
  • Placebo + Methotrexate: 30.4% (21/69) versus 52.2% (36/69) on control; risk difference -21.7 percentage points (95% CI -37.8 to -5.7), risk ratio 0.58 (0.38–0.89); unadjusted two-proportion z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Certolizumab Pegol 200 mg and Placebo + Methotrexate and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Placebo + Methotrexate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of ACR70 (American College of Rheumatology 70% Improvement) Responders at Week 34 in Patients Randomized at Week 18

• 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 200 mg and Placebo + Methotrexate: 30.0% (21/70) versus 37.7% (26/69) on control; risk difference -7.7 percentage points (95% CI -23.4 to 8.0), risk ratio 0.80 (0.50–1.27); unadjusted two-proportion z-test p = 0.339.
  • Placebo + Methotrexate: 15.9% (11/69) versus 37.7% (26/69) on control; risk difference -21.7 percentage points (95% CI -36.1 to -7.4), risk ratio 0.42 (0.23–0.79); unadjusted two-proportion z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Certolizumab Pegol 200 mg and Placebo + Methotrexate and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Placebo + Methotrexate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in DAS28 (Disease Activity Score-28 Items) at Week 34 in Patients Randomized at Week 18

• 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 errors.
• Result:
  • Certolizumab Pegol 200 mg and Placebo + Methotrexate: mean -2.83 versus -3.04 on control; difference 0.21 (95% CI -0.24 to 0.66), standardized effect d = 0.16; z-test p = 0.364.
  • Placebo + Methotrexate: mean -1.65 versus -3.04 on control; difference 1.39 (95% CI 0.93 to 1.85), standardized effect d = 1.02; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Certolizumab Pegol 200 mg and Placebo + Methotrexate and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Placebo + Methotrexate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes extend the primary response question in two ways: ACR50 and ACR70 use more stringent response thresholds, while change in DAS28 measures change on a disease activity scale. Across these outcome types, the posted pattern is broadly consistent with higher response percentages and greater improvement in the certolizumab groups than in the placebo group. The contrast between the two certolizumab schedules is less clear-cut in the posted unadjusted results. This overall pattern provides context for the primary ACR20 endpoint, but it does not replace the primary result or establish a single conclusion across all outcomes.

The registry record lists other secondary measures, including SDAI and CDAI change and remission outcomes, while the posted secondary results include 35 outcomes. It is important to distinguish outcomes listed in the registry from results actually available for interpretation. The posted secondary results do not include every endpoint named in the registry's secondary-outcome list. The record does not explain the difference or report a complete accounting of all analyses.

Secondary results generally carry less confirmatory weight when many outcomes or contrasts are examined without a reported multiplicity procedure. Even if an individual unadjusted result appears notable, the chance of seeing at least one apparently unusual result rises as more comparisons are considered. The registry record does not report a multiplicity adjustment or a hierarchy governing interpretation of secondary outcomes. Their unadjusted estimates are best treated as supportive or exploratory descriptions rather than independent confirmation of the primary finding.

The secondary measures also differ in scale and meaning. A responder percentage depends on a threshold, whereas change in DAS28 summarizes movement on a continuous scale. Agreement across different measures can add context, but it does not eliminate uncertainty from missing data, analysis choices, or multiple testing. The pattern should be read as a set of related observations within this trial, not as separate definitive conclusions for each endpoint.

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

• Percentage of ACR20 (American College of Rheumatology 20% Improvement) Responders at Week 16 in All Patients
• Percentage of ACR50 (American College of Rheumatology 50% Improvement) Responders at Week 16 in All Patients
• Percentage of ACR70 (American College of Rheumatology 70% Improvement) Responders at Week 16 in All Patients
• Change From Baseline in DAS28 (Disease Activity Score-28 Items) at Week 16 in All Patients
• Change From Baseline in SDAI (Simplified Disease Activity Index) at Week 16 in All Patients
• Change From Baseline in CDAI (Clinical Disease Activity Index) at Week 16 in All Patients
• DAS28 (Disease Activity Score-28 Items) Remission (DAS28 <2.6) at Week 16 in All Patients
• SDAI (Simplified Disease Activity Index) Remission (SDAI ≤3.3) at Week 16 in All Patients

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each patient is classified as an ACR20 responder or non-responder, and the reported arm result is a percentage. A risk difference expresses the contrast between two response proportions on the proportion scale. A value of zero corresponds to equal proportions; a positive or negative value indicates the direction of the contrast according to the comparison's group ordering. The sign must therefore be interpreted alongside which group is the reference and which is being compared. The confidence interval gives a range of values compatible with the data and calculation method, subject to the assumptions of that method.

What does non-responder imputation do?

The registry record states that missing values in the primary endpoint were imputed using non-responder imputation. In practical terms, a missing outcome is assigned to the non-responder category for this analysis. This provides a consistent way to include patients with missing Week 34 response data in the binary endpoint. It does not recover an unobserved response; it applies a particular assumption. If missingness is related to a patient's likely response, the resulting estimate may differ from an analysis using other assumptions. The registry record does not report sensitivity analyses or additional missing-data assumptions for this endpoint.

The primary analysis population is described as the full analysis set, with 208 patients included and the arm counts reported as 69, 70, and 69. This is distinct from the 333 patients described in the run-in overall. The record does not report the reasons for the difference between those populations. The estimand represented by the posted percentages is consequently tied to patients randomized at Week 18 and the stated non-responder imputation procedure, rather than all run-in participants regardless of randomization or endpoint availability.

What do the recalculated comparisons represent?

The contrasts and p-values discussed in the interpretation are unadjusted recalculations from the posted arm counts. They are not listed as sponsor-reported analyses in the registry record. A p-value describes how unusual a result at least as incompatible with the null hypothesis would be under the assumptions of the test; it is not the probability that the null hypothesis is true, and it does not measure the clinical importance of an effect. An unadjusted p-value also does not account for examining multiple outcomes or contrasts.

The 95% confidence interval for a risk difference describes uncertainty in the estimated contrast. When it includes zero, the data are compatible with no difference as well as with values on either side of zero at that confidence level. When it excludes zero, that is evidence against a zero contrast under the calculation assumptions, but it does not address bias, multiplicity, or whether the effect matters clinically. These intervals are based on posted summary data and should not be mistaken for adjusted trial-model estimates.

Why does the analysis population matter?

Trial outcomes can be defined for different populations, such as everyone randomized, everyone treated, or patients meeting an analysis-set definition. The registry record names a full analysis set and states which patients contribute to the primary analysis, but does not provide a more detailed population rule. Results from this set should not automatically be generalized to all 333 run-in participants. The record also does not report a detailed account of withdrawals, exclusions, adherence, or reasons for missing endpoint data.

Randomization supports comparisons between assigned groups by reducing systematic differences at assignment, on average. It does not guarantee that every observed group difference is caused by treatment, especially when the record does not provide full details of follow-up, missingness, protocol deviations, or analysis adjustments. Double masking is recorded, but the record does not describe the masking procedures or whether masking was maintained throughout follow-up.

What is not established by the registry record?

The registry record does not report the trial's original sample-size justification, detailed statistical analysis plan, prespecified contrasts, multiplicity adjustment, interim analyses, or sponsor-reported inferential results for the primary outcome. Those omissions matter when assessing whether the posted comparisons were primary to the analysis plan and how the trial handled multiple endpoints. The recalculated comparisons remain useful descriptive analyses of posted summary statistics, but they cannot substitute for an unavailable prespecified analysis plan or sponsor analysis.

11. Confidence Intervals and Precision

The arm percentages provide a compact description of the observed response pattern, but they are estimates based on finite groups. The risk-difference confidence intervals express how much uncertainty remains about the contrast. For the 200 mg group compared with the 400 mg group, the interval ranges from -0.138 to 0.176. Its inclusion of zero means that the unadjusted summary-data comparison is compatible with no difference as well as with differences in either direction. The point estimate alone should not be read as a precise estimate of how the regimens differ.

For placebo plus methotrexate compared with the 400 mg group, the interval ranges from -0.365 to -0.040. This interval lies below zero for the contrast as coded, corresponding to a lower observed response proportion in the placebo group. It still spans a range of possible contrast sizes, so it should not be reduced to a single fixed effect. The interval describes statistical uncertainty, not the probability that a particular value is correct.

Precision is influenced by the number of patients contributing to an analysis and by the amount of variation in the outcome. Binary outcomes contain limited information per participant compared with a continuous measurement, and estimates based on modest group sizes can remain uncertain. The primary analysis includes 69, 70, and 69 patients across the three groups. The registry record does not report sponsor-model confidence intervals for the primary outcome, so the intervals discussed are unadjusted recalculations from posted summaries.

Confidence intervals do not correct for multiple comparisons, selection of outcomes, missing-data assumptions, or limitations in generalizability. They also do not establish clinical importance. Reading the interval alongside the response percentages and analysis definition gives a more complete account than relying on the point estimate or p-value alone.

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 illustrations based on the observed effect, not the trial's original design calculations. For these binary outcome comparisons, the displayed sample sizes are participants per arm, not total participants across both groups and not total events. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The trial's own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm under those planning assumptions for an analysis to have an 80% chance of detecting the specified effect if that effect is the true one. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm. These are prospective planning quantities under a model, not descriptions of what happened in the completed trial.

Rows for 100%, 75%, and 50% of the observed effect illustrate how the required sample size changes when the target effect is smaller than the observed estimate. Smaller effects are harder to distinguish from random variation and need more participants to reach the same target power, all else equal. The figures can therefore be sensitive to the observed effect used as their starting point. If that estimate is uncertain, the planning illustrations inherit that uncertainty. The calculations are not observed power; they do not measure the probability that the completed trial's result was correct or that a treatment effect exists.

The sample-size curve should be read in the same planning context: it relates the assumed effect size to the number of participants needed under the stated assumptions. It is not a record of actual enrollment or a post hoc score for the trial. Values from such planning illustrations are most useful for understanding how assumptions about effect size and desired power influence a future design, rather than for judging the result by whether the completed trial matched an illustrative target.

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 = 0.652; treatment proportion p₁ = 0.671; average p̄ = 0.662.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6691 = 1.3113.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6689 = 0.5630.
4. n = (1.3113 + 0.5630)² / (0.0193)² = 9,475.7, rounded up to 9,476 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 <- 0.652173913043478                          # control proportion
p1 <- 0.671428571428571                          # 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(580840)
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 = 9,476 (80% power), 12,685 (90% power)
 75% of observed effect: n per arm = 16,905 (80% power), 22,631 (90% power)
 50% of observed effect: n per arm = 38,167 (80% power), 51,094 (90% power)
power.prop.test: 9475.7 
Simulated power at n = 9,476 per arm: 0.800 (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. Multiplicity, Missing Data and Analysis Populations

The trial reports a primary endpoint and numerous secondary outcomes. Each additional endpoint or comparison creates another opportunity for an apparently unusual result to arise by chance. A multiplicity strategy can control how much the overall chance of false-positive findings increases across a family of tests, for example by specifying a testing hierarchy or adjustment. A strategy of this kind is not reported in the registry record. The unadjusted recalculated p-values therefore should not be interpreted as though they account for all endpoints and comparisons in the trial.

The registry record identifies non-responder imputation for missing values in the primary endpoint. This is a clear analysis rule, but it treats missing outcomes as non-response and may not reflect every patient's unobserved status. The record does not report the amount or reasons for missing primary outcomes, nor does it report sensitivity analyses under alternative assumptions. Without those details, the influence of missing data on the response percentages cannot be fully assessed.

The primary analysis is described as including 208 patients in the full analysis set, whereas the run-in overall included 333. The record does not report why the numbers differ, what happened to patients not included in the randomized analysis, or whether further exclusions occurred. These details are relevant to understanding the analysis population and possible selection after the run-in. The registry record also does not report a detailed statistical analysis plan, interim-analysis procedures, or sponsor-reported inferential analyses for the posted endpoint.

These gaps do not make the posted outcome percentages unusable, but they constrain the strength of statistical claims. The primary percentages and unadjusted comparisons can be described as results under the stated population and imputation rule. Broader confirmatory interpretation would require information about prespecification, multiplicity, missing outcomes, and the full analysis process that is not reported in the registry record.

15. 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: musculoskeletal chest pain (1.4%), dermal cyst (1.4%), pneumonia (1.4%), coronary artery occlusion (1.4%), pericardial effusion (1.4%).

The registry record reports serious adverse events for the run-in overall and separately for the randomized groups. In the run-in overall, 18 of 333 patients were reported as having a serious adverse event. Among randomized patients, the corresponding figures were 2 of 69 in the 400 mg certolizumab pegol group, 5 of 70 in the 200 mg group, and 0 of 69 in the placebo group. These are counts of patients affected within each reported group, not rates adjusted for follow-up duration or exposure.

The record also reports other adverse events for 80 of 333 patients in the run-in overall, and for 20 of 69, 12 of 70, and 27 of 69 in the three randomized groups, respectively. A serious adverse event is a distinct reporting category from other adverse events, and the figures should not be added together because the record does not establish that the categories are mutually exclusive. The registry record does not report deaths for these groups.

The listed serious-event terms each have a reported frequency of 1.4%: musculoskeletal chest pain, dermal cyst, pneumonia, coronary artery occlusion, pericardial effusion, and pyrexia. The registry record does not provide enough detail in these figures to compare safety risks formally, account for differences in exposure or follow-up, or establish causation. These counts describe reported events in the recorded groups and should be interpreted as descriptive safety information.

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

The posted results describe ACR20 response at Week 34 among patients randomized at Week 18, with missing outcomes classified as non-response. The observed response percentages were higher in both certolizumab-containing groups than in the placebo group. The unadjusted comparison of the 200 mg schedule with the 400 mg schedule is imprecise, while the unadjusted comparison of placebo with the 400 mg group is compatible with a lower response proportion in the placebo group. These statements concern the endpoint and analysis definition in this record.

They do not establish that one certolizumab schedule is equivalent or non-inferior to the other. A non-significant difference is not proof of sameness, and the registry record does not report a prespecified equivalence or non-inferiority margin. Nor do the posted percentages establish effects on every rheumatoid arthritis outcome, effects beyond Week 34, or effects in patients unlike those included in the randomized analysis.

The result does not show how much each responding patient improved, because the primary endpoint classifies patients against a threshold. It does not explain individual response, guarantee a particular outcome for any patient, or establish that observed differences arose solely from assigned treatment. Inference is limited by the available population details, the missing-data rule, the absence of reported sponsor inferential analyses, and the lack of a reported multiplicity plan.

Accordingly, the most defensible reading is descriptive and comparative: the trial record contains higher observed ACR20 response percentages in the certolizumab groups than in the placebo group, with uncertainty around the contrasts and limited information about the full analysis process. The secondary results offer related context but carry less weight without a reported multiplicity strategy. The safety counts are also descriptive and do not provide a formal comparative risk analysis.

17. Why This Trial Matters Statistically

This trial illustrates how a clinical outcome can be both clinically interpretable and statistically incomplete. ACR20 translates multiple measurements into a responder percentage, making the result easy to state, while its threshold means the percentage does not show the full distribution of improvement. Reading the percentages together with risk-difference intervals makes the uncertainty more visible.

It also demonstrates why the analysis population and treatment timeline matter. The primary result concerns patients randomized at Week 18 after a run-in, rather than the full run-in enrollment. The record identifies non-responder imputation for missing primary outcomes, so the headline proportions depend on an explicit missing-data convention. Readers need both details to understand what the estimate represents.

The comparisons between the two certolizumab schedules and between a certolizumab group and placebo answer different questions. The interval for the schedule comparison is broad and includes zero; it does not establish equivalence. The placebo contrast has a different pattern, but its recalculated p-value is unadjusted and should not be treated as accounting for the many posted outcomes.

Finally, the record distinguishes posted descriptive results from sponsor-reported inferential analyses. No sponsor analyses are reported for these results, and important design details, including the original sample-size justification and multiplicity plan, are not reported. This makes the trial a useful example of how to interpret registry data carefully: describe what the estimates show, identify the assumptions behind them, and avoid claims that the record cannot support.

18. 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 limitations specific to this record affect interpretation. The primary analysis uses patients randomized at Week 18 after a run-in, while the overall run-in enrollment was 333 and the primary analysis included 208. The registry record does not explain the difference, identify reasons for non-randomization or exclusion, or describe all participant flow. This limits understanding of how the randomized analysis population relates to everyone who entered the study.

The primary endpoint uses non-responder imputation, but the record does not report the number or pattern of missing Week 34 values, reasons for missingness, or sensitivity analyses. The posted result may depend on this assumption. The record also does not report sponsor inferential analyses for the primary outcome; the displayed comparisons discussed in the statistical interpretation are unadjusted recalculations from summary counts.

The registry record does not report the original sample-size justification, detailed statistical analysis plan, prespecified testing hierarchy, multiplicity adjustment, or interim-analysis approach. Because numerous secondary outcomes are posted, absence of a reported multiplicity plan makes isolated unadjusted findings less persuasive as confirmatory evidence. The record lists secondary outcomes at Week 16, while posted secondary results include Week 34 outcomes; it does not explain that difference.

There is no direct inferential comparison reported between the two certolizumab schedules in the posted recalculated contrasts; each is compared with the 400 mg reference as encoded in the results. The registry record also does not give enough detail to assess adherence, treatment discontinuation, protocol deviations, masking procedures, or the duration of exposure for safety comparisons. These limits constrain conclusions about treatment differences, generalizability, and comparative safety.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Dosing Flexibility Study in Patients With Rheumatoid Arthritis — NCT00580840.
• Registry record last updated 2018-08-02; status last verified 2012-03.
• Results first posted 2012-03-19.
• 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.

22. Record Summary

The registry record describes a completed Phase 4 randomized, double-blind, parallel-group study of certolizumab pegol with methotrexate in active rheumatoid arthritis. A run-in preceded randomization at Week 18. The primary endpoint was ACR20 response at Week 34 among 208 randomized patients, analyzed with non-responder imputation.

Observed response percentages were 65.2% for the 400 mg certolizumab pegol group, 67.1% for the 200 mg group, and 44.9% for placebo, each alongside methotrexate. Unadjusted recalculated contrasts show an imprecise comparison between the certolizumab schedules and a lower response proportion in the placebo group relative to the 400 mg group. The registry record does not report sponsor inferential analyses, the original sample-size justification, or a multiplicity plan. Safety counts are descriptive. Interpretation is therefore limited to the posted outcomes, analysis population, and stated missing-data rule.