Study to Evaluate Maintenance of Sustained Remission of axSpA With CZP Compared to Placebo: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate Maintenance of Sustained Remission of axSpA With CZP Compared to Placebo (NCT02505542), a randomized phase 3 study. The primary outcome is Percentage of Participants in Part B Who Did Not Experienced a Flare.

2. Clinical Question

This is a maintenance question in a selected group, not a question about the initial response to treatment across all 736 enrolled participants. Entry into Part B required sustained remission following open-label treatment in Part A. Consequently, the randomized comparison concerns subsequent outcomes among those who met that remission condition, rather than among all people who might begin treatment.

3. Trial Design

The registry describes a completed phase 3, randomized, double-blind, parallel-group study sponsored by UCB BIOSCIENCES GmbH. It had two parts. Part A was open-label: participants received certolizumab pegol for 48 weeks. The listed schedule began with 400 mg at Weeks 0, 2 and 4, followed by 200 mg every 2 weeks from Week 6 to Week 48. Participants who reached sustained remission could qualify for randomization into Part B.

Part B compared placebo with certolizumab pegol 200 mg every 2 weeks or every 4 weeks, from Week 48 onwards. It was double-blind, with placebo injections used at visits when needed to preserve masking. The randomized set comprised 104 participants in the placebo group, 104 in the every-2-weeks group, and 105 in the every-4-weeks group. The registry reports total enrollment of 736, which is distinct from the smaller population randomized in Part B.

The primary outcome covered Week 48 to Week 96 and was assessed in the randomized set. Participants could receive escape treatment after meeting flare criteria. The registry describes escape from placebo to open-label certolizumab pegol and dose-schedule changes after flare in the active-treatment groups. How those treatment changes were handled in every analysis is not reported in the registry record.

The registry lists the study start as 2015-07, primary completion as 2019-02, and status as completed. Details of the original sample-size justification, planned interim analyses, randomization procedures, 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: The study included 2 parts: Part A with a Screening Period (up to 5 Weeks) and an Open-Label Period (Week 0 to Week 48) and Part B with a Double-Blind Period (Week 48 to Week 96) and a Safety Follow-Up Period (10 weeks after the last dose of study medication). Participant Flow refers to the Open-Label Set.

Part A: Open-Label Period

Reasons for not completing this period:

Completed Part A, Did Not Enter Part B

Reasons for not completing this period:

Part B: Double-Blind Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Randomized Set (RS) consisted of all study participants randomized into Part B of the study.

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 Characteristics refer to the The Open-Label Set (OLS) which consisted of all study participants who received at least 1 dose of investigational medicinal product (IMP) in the Open-Label Period of the study (Part A).

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants in Part B Who Did Not Experienced a Flare, measured over From Week 48 to Week 96.

The primary endpoint was the percentage of participants in Part B who did not experience a flare from Week 48 to Week 96. A flare was defined as an ASDAS of at least 2.1 at 2 consecutive visits or an ASDAS greater than 3.5 at any visit during Part B up to Week 96. The endpoint therefore describes the proportion meeting the registry’s no-flare classification over the specified follow-up, rather than a continuous change in disease activity.

Part B eligibility depended on sustained remission after 48 weeks of open-label certolizumab pegol. Sustained remission required an ASDAS less than 1.3 at Week 48 and qualifying values at Week 32 or Week 36 under the stated criteria. This makes the primary question specifically about maintaining remission among participants who first achieved the required state; it does not describe outcomes for everyone enrolled in Part A.

A binary endpoint such as this can be summarized as a percentage in each randomized group and compared using a difference in proportions or a model-based measure such as an odds ratio. The registry reports the group percentages and a logistic-regression analysis. Missing data were handled using non-response imputation (NRI), according to the endpoint description. The registry’s more detailed operational rules for missing values are not reported in the registry record.

7. Results Posted in the Registry

• Certolizumab Pegol 200 mg Q2W Double-Blind (RS): 83.7% (87/104) versus 20.2% (21/104) on control; risk difference 63.5 percentage points (95% CI 53.0 to 74.0), risk ratio 4.14 (2.80–6.13); unadjusted two-proportion z-test p = <0.001.
• Certolizumab Pegol 200 mg Q4W Double-Blind (RS): 79.0% (83/105) versus 20.2% (21/104) on control; risk difference 58.9 percentage points (95% CI 47.9 to 69.8), risk ratio 3.91 (2.64–5.81); 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 Participants With Axial SpondyloArthritis International Society 20 % Response Criteria (ASAS20) Response at Week 96 in Part B

• 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 Q2W Double-Blind (RS): 85.6% (89/104) versus 23.1% (24/104) on control; risk difference 62.5 percentage points (95% CI 52.0 to 73.0), risk ratio 3.71 (2.59–5.31); unadjusted two-proportion z-test p = <0.001.
  • Certolizumab Pegol 200 mg Q4W Double-Blind (RS): 78.1% (82/105) versus 23.1% (24/104) on control; risk difference 55.0 percentage points (95% CI 43.7 to 66.3), risk ratio 3.38 (2.35–4.88); 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 200 mg Q2W Double-Blind (RS) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Certolizumab Pegol 200 mg Q4W Double-Blind (RS) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Axial SpondyloArthritis International Society 40 % Response Criteria (ASAS40) Response at Week 96 in Part B

• 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 Q2W Double-Blind (RS): 84.6% (88/104) versus 21.2% (22/104) on control; risk difference 63.5 percentage points (95% CI 53.0 to 73.9), risk ratio 4.00 (2.74–5.85); unadjusted two-proportion z-test p = <0.001.
  • Certolizumab Pegol 200 mg Q4W Double-Blind (RS): 73.3% (77/105) versus 21.2% (22/104) on control; risk difference 52.2 percentage points (95% CI 40.6 to 63.7), risk ratio 3.47 (2.35–5.11); 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 200 mg Q2W Double-Blind (RS) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Certolizumab Pegol 200 mg Q4W Double-Blind (RS) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Axial SpondyloArthritis International Society (ASAS) 5/6 Response Criteria Response at Week 96 in Part B

• 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 Q2W Double-Blind (RS): 70.2% (73/104) versus 12.5% (13/104) on control; risk difference 57.7 percentage points (95% CI 46.8 to 68.5), risk ratio 5.62 (3.33–9.48); unadjusted two-proportion z-test p = <0.001.
  • Certolizumab Pegol 200 mg Q4W Double-Blind (RS): 62.9% (66/105) versus 12.5% (13/104) on control; risk difference 50.4 percentage points (95% CI 39.1 to 61.6), risk ratio 5.03 (2.96–8.54); 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 200 mg Q2W Double-Blind (RS) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Certolizumab Pegol 200 mg Q4W Double-Blind (RS) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary response outcomes at Week 96 follow the same broad pattern as the primary result: the reported response percentages are higher in both certolizumab pegol groups than in the placebo group for ASAS20, ASAS40, and ASAS 5/6. This directional consistency provides related context for the primary no-flare finding, but these endpoints measure response criteria rather than the primary endpoint’s maintenance of no flare. They should therefore be interpreted as complementary outcomes, not as interchangeable measures.

The registry lists other secondary outcomes, including ASDAS disease activity and clinical improvement categories, sustained remission at Week 48, and time to flare. Detailed result values for those outcomes are not reported in the registry record. The listed endpoints cover different aspects of disease activity and response, so the overall secondary-outcome pattern cannot be fully evaluated from the available results.

Each additional outcome or comparison creates another opportunity for a statistically significant result to arise by chance when many tests are conducted. Unless a multiplicity procedure is specified, nominal p-values from secondary analyses carry less confirmatory weight than a result from a prespecified primary analysis. Whether multiplicity adjustment or a formal testing hierarchy was used is not reported in the registry record. The secondary findings should accordingly be read as supportive or exploratory rather than as independent proof of the primary conclusion.

As with the primary outcome, the secondary comparisons concern the selected randomized population and are subject to the study’s missing-data and follow-up rules. The registry’s summary does not establish how every secondary endpoint handled missing values or escape treatment; those details are not reported in the registry record.

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

• Percentage of Participants Achieving Sustained Remission at Week 48 in Part A
• Percentage of Participants in Ankylosing Spondylitis Disease Activity Score (ASDAS) Disease Activity Categories at Week 48 in Part A
• Percentage of Participants in Ankylosing Spondylitis Disease Activity Score (ASDAS) Clinical Improvement Categories at Week 48 in Part A
• Time to Flare in Part B
• Percentage of Participants in Ankylosing Spondylitis Disease Activity Score (ASDAS) Disease Activity Categories at Week 96 in Part B
• Percentage of Participants in Ankylosing Spondylitis Disease Activity Score (ASDAS) Clinical Improvement Categories at Week 96 in Part B
• Percentage of Participants With Axial SpondyloArthritis International Society 20 % Response Criteria (ASAS20) Response at Week 96 in Part B
• Percentage of Participants With Axial SpondyloArthritis International Society 40 % Response Criteria (ASAS40) Response at Week 96 in Part B

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: each participant is classified according to whether they did or did not experience a flare during Part B. A group percentage is the proportion classified as not experiencing a flare. A risk difference compares two such proportions by subtracting one proportion from the other. Its scale is an absolute difference in probability, whereas a risk ratio compares proportions as a ratio and an odds ratio compares the odds of the outcome.

The recalculated risk differences are unadjusted comparisons based on the posted group summaries. “Unadjusted” means that the calculation does not account for covariates through a regression model. The estimates and confidence intervals are useful descriptive comparisons, but they are not replacements for the sponsor’s prespecified or model-based analysis. The registry’s reported primary analyses used logistic regression and reported odds ratios.

What does a logistic-regression odds ratio describe?

Logistic regression models the log odds of a binary outcome. Exponentiating a model coefficient gives an odds ratio for the comparison represented by that coefficient. An odds ratio above 1 indicates higher modeled odds of the defined outcome in the first group relative to the reference group, given the model’s coding. Odds are not the same as probabilities, so an odds ratio should not be interpreted as a risk difference or as a multiple of the group percentage. The registry identifies placebo as the comparator and reports the odds ratios for the active-treatment groups versus placebo.

The registry reports two-sided statistical evidence as p < 0.001 for both primary comparisons. A p-value describes how incompatible the observed data are with a specified null model under the test assumptions; it is not the probability that the null hypothesis is true, nor does it measure the size or importance of the observed difference. The registry’s exact model covariates and detailed test specification are not reported in the registry record.

Why use confidence intervals?

A confidence interval gives a range of values compatible with the data and the method used, under repeated use of that method. For a group percentage, it conveys uncertainty about the population percentage represented by the randomized participants. For a risk difference or odds ratio, it conveys uncertainty about the corresponding comparison. A narrow interval indicates greater precision than a wide interval on the same scale, but interval width alone does not determine whether an effect is clinically meaningful.

How does the endpoint rule affect classification?

The flare definition uses thresholds at one or more visits: ASDAS at least 2.1 at 2 consecutive visits, or greater than 3.5 at any visit during Part B up to Week 96. A participant’s classification therefore depends on the observed sequence of assessments and the registry’s handling of missing assessments. The endpoint description states that NRI was used. In general, non-response imputation assigns missing outcome information to the non-response category; the precise implementation for each missing-data pattern is not reported in the registry record.

The population is also central to the method. Only participants who achieved the specified sustained remission after open-label treatment could qualify for Part B, and the primary analysis used the randomized set. The comparison is consequently conditional on reaching that stage and qualifying for randomization. The registry does not report the full details of the statistical analysis plan, including model covariates, multiplicity procedures, or sensitivity analyses, so those aspects cannot be assessed from the record.

Why does over-dispersion matter?

General explanation: over-dispersion occurs when observed variability is greater than a statistical model expects. It matters when a model’s uncertainty estimates rely on a variance assumption that is too restrictive; standard errors and confidence intervals can then be too small. The primary outcome is binary and the registry reports logistic regression, but whether over-dispersion was assessed or relevant to the sponsor’s specific model is not reported in the registry record.

11. Confidence Intervals and Precision

The registry reports 95% confidence intervals for the primary group percentages. For placebo, the estimate was 20.2% with a 95% confidence interval from 13.0% to 29.2%. For certolizumab pegol 200 mg Q2W, it was 83.7% (75.1% to 90.2%), and for 200 mg Q4W it was 79.0% (70.0% to 86.4%). These intervals describe uncertainty around the group percentages, not the range of individual participant outcomes.

The unadjusted risk-difference interval for Q2W versus placebo was 0.530 to 0.740 around an estimate of 0.635. For Q4W versus placebo, the interval was 0.479 to 0.698 around an estimate of 0.589. Both intervals lie on the positive side of zero. The sponsor’s model-based odds-ratio intervals were 9.605 to 38.864 for Q2W versus placebo and 7.395 to 27.955 for Q4W versus placebo. These intervals are on the odds-ratio scale and are not directly comparable in size to the risk-difference intervals.

The group estimates are based on 104, 104, and 105 participants, respectively. Confidence intervals express sampling uncertainty under the calculation method; they do not account for every possible source of uncertainty, such as limitations in generalizability or the choice of missing-data approach. The registry does not report a confidence interval for a direct comparison between the two active schedules.

General explanation: confidence intervals do not mean that there is a 95% probability that a particular fixed parameter lies within the interval after the data have been observed. Rather, a 95% interval procedure would cover the fixed parameter in 95% of repeated samples if its assumptions hold. The interval’s interpretation depends on the analysis method and the study population.

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 illustrations report participants per arm for the binary comparisons, not total events. They use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These are planning assumptions for illustrations based on the observed result; the trial’s original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm under those assumptions for an 80% chance of detecting the specified effect if that effect is the true one. The 90% power column gives the corresponding number per arm for a 90% chance. For example, the rows describe planning for 100%, 75%, or 50% of the observed effect. They do not represent the trial’s observed power or its actual enrollment requirement.

Smaller effects require more participants to detect with the same significance level and power, all else held constant. That pattern is reflected by the larger planning counts for smaller fractions of the observed effect. The illustrations are sensitive to their assumptions, including the event rates used and the effect chosen for planning. They should not be read as evidence that the trial was designed using these calculations or that the same numbers apply to a future study with different participants, outcome rates, or analysis methods.

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 = 0.202; treatment proportion p₁ = 0.837; average p̄ = 0.519.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7066 = 1.3849.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5458 = 0.4594.
4. n = (1.3849 + 0.4594)² / (0.6346)² = 8.4, rounded up to 9 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 <- 0.201923076923077                          # control proportion
p1 <- 0.836538461538462                          # 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(2505542)
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 (80% power), 11 (90% power)
 75% of observed effect: n per arm = 16 (80% power), 21 (90% power)
 50% of observed effect: n per arm = 35 (80% power), 47 (90% power)
power.prop.test: 8.4 
Simulated power at n = 9 per arm: 0.822 (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’s own primary analysis used logistic regression and reported odds ratios of 18.822 for certolizumab pegol 200 mg Q2W versus placebo and 14.069 for 200 mg Q4W versus placebo. The corresponding 95% confidence intervals were 9.605 to 38.864 and 7.395 to 27.955, and both reported p-values were < 0.001. The registry labels both comparisons as superiority analyses.

The recalculated comparisons use the posted group summaries to estimate unadjusted risk differences: 0.635 for Q2W versus placebo and 0.589 for Q4W versus placebo. These answer the comparison on a different scale and do not adjust for covariates. They are useful as a straightforward description of the observed group percentages, but they are not the sponsor’s regression estimates.

There is no reported discrepancy between the posted group summaries and the sponsor’s analyses. For inferential interpretation, the sponsor’s own analysis takes precedence over a simple recalculation from summary statistics. The registry does not report enough detail to reproduce the logistic-regression model independently, including all model specifications and covariates.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint description states that missing data were handled using non-response imputation (NRI). In general, NRI treats missing outcome information as non-response for a binary response endpoint. This approach can make the result depend on the amount and pattern of missing information, as well as on how the imputation rule is applied. The registry record does not report the number of missing primary endpoint assessments, the detailed implementation of NRI, or sensitivity analyses testing alternative assumptions.

The registry reports 35 outcome measures, 30 analyses, and 34 posted secondary outcomes. Testing multiple outcomes and comparisons can increase the chance of at least one nominally significant finding even when no true effect exists. The record does not report whether p-values were adjusted for multiplicity, whether a hierarchy controlled the testing sequence, or whether the secondary analyses were designated as confirmatory or exploratory. The reported p-values should be interpreted in that context.

The primary population was the randomized set: participants randomized into Part B after meeting the sustained-remission eligibility condition. This is not the same population as all enrolled participants. The primary endpoint description makes the Part B eligibility condition explicit, but additional analysis-population definitions or exclusions are not reported in the registry record.

Participants who met flare criteria could receive escape treatment, with the registry describing treatment changes for placebo and active-treatment groups. The extent to which escape treatment affected endpoint classification, censoring, or analysis is not reported in the registry record. Nor are detailed sensitivity analyses, subgroup analyses, or the complete statistical analysis plan reported. These omissions limit assessment of the robustness of the results to missingness, post-randomization treatment changes, and analytical choices.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

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: irritable bowel syndrome (16.7%), pancreatitis acute (1.0%), crohn's disease (1.0%), intestinal obstruction (1.0%), anal abscess (1.0%).

The registry reports serious adverse events for the open-label Part A group and the double-blind Part B groups. In Part A, 44 serious adverse events were reported among 736 participants at risk during Weeks 0–48. In Part B, the reported counts were 0 among 103 at risk in the placebo group, 5 among 104 in the Q2W group, and 0 among 105 in the Q4W group during Weeks 48–96. These are counts in the registry’s listed safety groups; they are not estimates of comparative treatment effects.

The Part B safety denominator for placebo is 103, while the primary randomized-set denominator is 104. The registry record does not explain this difference. No deaths are listed in any of the reported safety groups. Serious adverse events are distinct from the broader category of other adverse events, which the registry reports separately; the Part A other-adverse-event count was 188 among 736, and the Part B counts were 25 among 103, 31 among 104, and 26 among 105, respectively.

These counts should be interpreted with the group definitions and observation periods in mind. The Part A period was open-label, and the Part B groups had different treatment assignments and denominators. The registry’s figures alone do not establish causation or support a full comparative safety assessment.

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

The result describes the percentage of participants in the Part B randomized set who met the registry’s definition of not experiencing a flare from Week 48 to Week 96. The reported percentages were higher in both certolizumab pegol groups than in the placebo group. The sponsor’s logistic-regression analyses report p < 0.001 for each active-treatment comparison with placebo, with confidence intervals that express uncertainty around the odds-ratio estimates.

The result does not describe all participants who entered the study. Part B was restricted to participants who achieved sustained remission after open-label treatment, so the finding applies to a selected population that met this condition. It does not answer how often remission would be achieved in all participants beginning Part A, nor does it establish outcomes for people who would not qualify for Part B.

The result also does not establish that one active dose schedule is better than the other. The registry reports comparisons of each active group with placebo, but a direct active-versus-active primary comparison is not reported in the registry record. Similar-looking percentages or overlapping confidence intervals are not a substitute for a formal comparison between the active groups.

Statistical evidence is not the same as a complete account of clinical importance. The primary endpoint is a binary classification based on ASDAS thresholds and visit timing, and the registry’s analysis used NRI for missing data. The result therefore depends on that definition and analysis approach. It does not establish what would happen with another endpoint, another follow-up period, or another population.

Finally, this outcome should not be interpreted as a complete summary of benefit, risk, or long-term outcomes. The posted results cover specified outcomes and periods, and some details of the analysis and missing-data handling are not reported in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates the importance of distinguishing an induction population from a maintenance population. All 736 enrolled participants are not the denominator for the primary Part B comparison. Randomization occurred after open-label treatment and after participants met a sustained-remission condition, producing a specific population for the maintenance question. Clear identification of that population is essential for interpreting both the percentages and their scope.

It also demonstrates why a statistical measure must be named and interpreted on its own scale. The registry reports logistic-regression odds ratios, while a simple recalculation from the group summaries yields risk differences. Both describe the same underlying comparison from different perspectives, but they are not numerically interchangeable. Reporting group percentages alongside comparison estimates and confidence intervals helps readers understand the outcome scale and the uncertainty.

The binary endpoint uses a defined threshold-based flare rule, and missing data were handled with NRI. Those choices influence classification and therefore the estimated percentages. The presence of escape treatment further emphasizes the value of knowing how post-randomization events are incorporated into an endpoint analysis; that detail is not reported in the registry record.

Finally, the registry’s primary result is accompanied by several secondary outcomes and comparisons. Without reported multiplicity procedures, secondary p-values warrant more cautious interpretation. Together, these features show why statistical interpretation depends not only on the observed percentages, but also on who was analyzed, how outcomes were defined, how missing information was handled, and which comparisons were planned.

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.

The primary analysis concerns a selected Part B population: participants had to achieve sustained remission during open-label treatment before qualifying for randomization. This limits direct generalization to all 736 enrolled participants and to people who would not meet that condition. The registry does not report demographic or clinical characteristics needed to assess how closely the randomized participants represent other populations.

The endpoint is a threshold-based binary measure that depends on ASDAS values across visits. The registry describes the flare rule and NRI, but the number and pattern of missing assessments and the detailed implementation of NRI are not reported in the registry record. Sensitivity analyses using alternative missing-data assumptions are also not reported.

Escape treatment was permitted after flare criteria were met. The registry describes the treatment changes, but does not report in the record how escape treatment was incorporated into each endpoint analysis. This is relevant because treatment changes occur after randomization and may affect interpretation of later outcomes.

The registry reports sponsor logistic-regression estimates but not the full model specification, including all covariates. It also does not report the original sample-size justification, detailed multiplicity procedures, planned interim analyses, or the complete statistical analysis plan. The secondary results available in the record do not cover every listed outcome in detail. A direct primary comparison between the Q2W and Q4W schedules is not reported.

These limitations do not alter the posted estimates, but they constrain what can be concluded from them and how fully the analyses can be independently assessed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate Maintenance of Sustained Remission of axSpA With CZP Compared to Placebo — NCT02505542.
• Registry record last updated 2020-12-17; status last verified 2020-11.
• Results first posted 2020-04-21.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT02505542 is a completed phase 3 randomized, double-blind, parallel-group study of certolizumab pegol and placebo in axial spondyloarthritis. Part A used open-label certolizumab pegol; participants who achieved sustained remission could enter Part B and be randomized to placebo, certolizumab pegol 200 mg Q2W, or 200 mg Q4W.

The primary Part B endpoint was the percentage who did not experience a flare from Week 48 to Week 96. The reported percentages were 20.2% for placebo, 83.7% for Q2W, and 79.0% for Q4W. The registry’s logistic-regression analyses reported odds ratios of 18.822 and 14.069, respectively, for the active groups versus placebo, with p < 0.001 for both comparisons.

The registry states that missing data were handled using NRI. Interpretation is specific to the randomized participants who first qualified through sustained remission, and the record does not report several details needed to assess the full statistical plan, multiplicity handling, or sensitivity to missing-data assumptions.