A Study to Evaluate the Efficacy and Safety of Dapirolizumab Pegol in Study Participants With Moderately to Severely Active Systemic Lupus Erythematosus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Efficacy and Safety of Dapirolizumab Pegol in Study Participants With Moderately to Severely Active Systemic Lupus Erythematosus (NCT04294667), a randomized phase 3 study. The primary outcome is Percentage of Participants With Achievement of BILAG 2004-based Composite Lupus Assessment (BICLA) Response at Week 48.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, quadruple-masked, parallel-group, placebo-controlled study sponsored by UCB Biopharma SRL. It evaluated dapirolizumab pegol as an add-on to standard-of-care medication for participants with moderately to severely active systemic lupus erythematosus. The registry lists 321 participants enrolled. The study is marked completed, with a start date of 2020-08-12 and primary completion date of 2024-05-22.

Participants were assigned to DZP plus standard of care or placebo plus standard of care. The registry’s arm descriptions state that participants received their assigned DZP or placebo throughout the Treatment Period. The record labels the study randomized and parallel-group; it also records quadruple masking. It does not identify which roles were masked in the registry record, nor does it report further details of the randomization procedure in the information available for this analysis.

The primary outcome was the percentage of participants achieving BICLA response at Week 48. The primary analysis population was the Full Analysis Set, defined as all randomized participants other than 6 participants excluded for persistent Good Clinical Practice non-compliance at the enrolling site. The arm summaries for this endpoint report 107 participants in the placebo-plus-standard-of-care group and 208 in the DZP-plus-standard-of-care group. These endpoint analysis counts should not be confused with the separately reported safety populations.

The registry also lists secondary outcomes covering BICLA response at earlier visits, severe BILAG flare prevention, disease activity, and other response measures. The study’s original sample-size assumptions, detailed allocation process, dosing schedule, 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: Participant flow refers to the Randomized Set (RS).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) consisted of all study participants randomized into the study except 6 participants excluded from FAS due to persistent Good Clinical Practice (GCP) non-compliance at the site enrolling them.

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 Safety Set (SS) which consisted of all study participants who were randomized and had received at least 1 dose (any amount) of study medication.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Achievement of BILAG 2004-based Composite Lupus Assessment (BICLA) Response at Week 48, measured over Week 48.

The primary endpoint is the percentage of participants achieving BICLA response at Week 48. BICLA is a composite measure: a participant had to meet every listed condition to count as a responder. The BILAG 2004 component required improvement in baseline A or B scores, no new A scores, and no more than 1 new B score. The scale distinguishes severely active disease (A), moderately active disease (B), mild stable disease (C), and inactive disease that was previously active (D).

In addition, the participant could not have an increase in the SLEDAI-2K total score from baseline. The Physician’s Global Assessment could not worsen by more than 10 mm on a 100 mm visual analog scale. Thus, response required improvement on the BILAG measure without worsening on either of the other measures under the stated rules.

A composite can capture more than one dimension of disease activity while requiring that improvement on one measure is not accompanied by specified worsening on others. That is a general reason composite endpoints are used. Here, the registry-defined response is a threshold-based outcome: each participant is classified as a responder or not a responder according to the complete set of criteria. The reported endpoint percentage therefore describes the proportion meeting that combined definition, not the average change in any single disease measure.

7. Results Posted in the Registry

• DZP+SOC: 49.5% (103/208) versus 34.6% (37/107) on control; risk difference 14.9 percentage points (95% CI 3.7 to 26.2), risk ratio 1.43 (1.07–1.92); unadjusted two-proportion z-test p = 0.011.

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 Achievement of BICLA Response at Week 24

• 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:
  • DZP+SOC: 46.6% (97/208) versus 38.3% (41/107) on control; risk difference 8.3 percentage points (95% CI -3.1 to 19.8), risk ratio 1.22 (0.92–1.61); unadjusted two-proportion z-test p = 0.159.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DZP+SOC and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Achievement of BICLA Response at Week 12

• 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:
  • DZP+SOC: 39.9% (83/208) versus 29.0% (31/107) on control; risk difference 10.9 percentage points (95% CI 0.1 to 21.8), risk ratio 1.38 (0.98–1.94); unadjusted two-proportion z-test p = 0.056.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DZP+SOC and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Achievement of Prevention of Severe British Isles Lupus Assessment Group (BILAG) Flares (Severe BILAG Flare-free) Through Week 48

• 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:
  • DZP+SOC: 88.5% (184/208) versus 76.6% (82/107) on control; risk difference 11.8 percentage points (95% CI 2.7 to 20.9), risk ratio 1.15 (1.03–1.30); unadjusted two-proportion z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for DZP+SOC than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several related but distinct aspects of disease activity and response. The reported pattern includes higher DZP-arm percentages for the posted BICLA assessments at earlier visits and for prevention of severe BILAG flares through Week 48. Other listed secondary measures include low disease activity, changes in disease activity scores, BILAG improvement, Physician’s Global Assessment, and SRI-4 response. Their definitions and follow-up windows differ, so the full set should be viewed as complementary rather than as multiple measurements of exactly the same outcome.

These secondary findings broadly relate to the primary Week 48 result by examining response at other times or using additional disease measures. They can help describe whether the overall pattern extends beyond the primary endpoint, but they do not replace it. Differences in the underlying criteria, measurement scale, and time point mean that agreement or disagreement across outcomes is not necessarily a direct contradiction.

Unadjusted secondary results carry less weight because multiple outcomes and comparisons create more opportunities for apparently notable results to occur by chance. The registry record does not report a multiplicity-control procedure or identify which secondary analyses, if any, were intended to be confirmatory. Their p-values should therefore be treated as nominal evidence for individual comparisons, not as proof that the entire collection of outcomes meets a single error-controlled standard.

The registry lists 15 secondary outcomes as posted, while the listed outcome set also includes measures for which results may not be present in the summary information. Reasons for any absent results are not reported in the registry record. A complete interpretation of the secondary program would require the prespecified hierarchy, analysis populations, missing-data methods, and multiplicity strategy.

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

• Percentage of Participants With Achievement of BICLA Response at Week 24
• Percentage of Participants With Achievement of BICLA Response at Week 12
• Percentage of Participants With Achievement of Prevention of Severe British Isles Lupus Assessment Group (BILAG) Flares (Severe BILAG Flare-free) Through Week 48
• Percentage of Participants With Achievement of Lupus Low Disease Activity State (LLDAS) in ≥50% of Post-Baseline Visits Through Week 48
• Change From Baseline in Systemic Lupus Erythematosus Disease Activity Index 2000 (SLEDAI-2K) at Week 48
• Percentage of Participants With Achievement of BILAG Improvement Without Worsening at Week 48
• Change From Baseline in Physician's Global Assessment (PGA) at Week 48
• Percentage of Participants With Achievement of Systemic Lupus Erythematosus Responder Index Response - 4 (SRI-4) Response at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant either met the complete BICLA response definition by Week 48 or did not. The arm percentages describe the proportion classified as responders. A comparison of two such proportions is commonly expressed as a risk difference, meaning the response proportion in one group minus the response proportion in the reference group. A difference above zero indicates a larger observed response proportion in the first group, using the stated comparison direction.

What does the reported analysis do?

The registry names the Cochran-Mantel-Haenszel method and reports a difference in proportions, a confidence interval, and a p-value for the primary comparison. In general, the Cochran-Mantel-Haenszel approach can combine evidence across strata while accounting for stratification. The registry record does not identify the stratification variables or provide enough detail to describe precisely how the sponsor implemented the method. It is therefore appropriate to report the named method without inferring the factors included in the analysis.

The reported difference is 14.6 percentage points, with a 95% confidence interval from 3.3 to 25.8 percentage points. The p-value is 0.011. In general, a p-value measures how incompatible the observed data are with a specified null hypothesis under the assumptions of the test; it is not the probability that the null hypothesis is true, nor a measure of the size or clinical importance of an effect. The interval adds information about the range of effect sizes reasonably compatible with the data under the method’s assumptions.

What is the role of an unadjusted recalculation?

A simple recalculation from posted group counts estimates the difference without reproducing possible stratification or other elements of the sponsor’s method. Such a calculation is a useful consistency check, not a replacement for the trial’s analysis. In this case the record does not flag a discrepancy, and the recalculated result is close to the sponsor-reported comparison. The sponsor’s own analysis remains the primary result. The registry’s reported method and result should not be described as adjusted for particular covariates unless those covariates are identified.

The outcome percentages and analysis populations also matter. For the primary endpoint, the Full Analysis Set excluded 6 randomized participants because of persistent Good Clinical Practice non-compliance at their enrolling site. The registry reports endpoint group counts of 107 and 208, while the safety groups have different counts. These are distinct analysis populations and denominators; they should not be substituted for one another.

How should confidence intervals be understood?

In general, a confidence interval represents the uncertainty of an estimate under a statistical procedure. It is not a range containing a fixed proportion of individual participant outcomes. For a difference in proportions, an interval that includes zero is compatible with no difference under the model and procedure used; an interval entirely on one side of zero is not. This interpretation depends on the analysis assumptions, endpoint ascertainment, and treatment of missing data.

The primary interval is entirely above zero, while the reported intervals for some secondary comparisons include zero and others do not. Those comparisons are not automatically confirmatory: the outcomes are multiple, and the registry record does not report whether or how multiplicity was controlled. A nominal p-value for a secondary result should therefore be read as evidence for that particular comparison under its stated test, not as a definitive conclusion across all secondary outcomes.

Finally, the planning illustrations use observed effects and stated assumptions rather than the trial’s original design calculations. They describe hypothetical participant requirements for detecting selected fractions of observed effects under a general calculation. They do not provide observed power or reveal the assumptions used when this Phase 3 study was designed.

11. Confidence Intervals and Precision

The primary comparison is estimated as a 14.6 percentage-point difference in BICLA response at Week 48, with a 95% confidence interval from 3.3 to 25.8 percentage points. The interval gives a sense of the statistical precision: it is compatible with a range of positive differences, rather than identifying one exact value. Since the entire reported interval is above zero, the sponsor’s analysis indicates a difference in favor of the DZP-plus-standard-of-care group for this endpoint under the stated method.

Precision is not the same as certainty about every relevant question. The interval concerns the estimated group contrast, not the response of any particular participant, and it does not account for unreported sources of uncertainty such as limitations in endpoint measurement or missing-data handling. Nor does it establish whether the magnitude is clinically important; the registry record does not specify a threshold for clinical importance.

The secondary estimates are less uniform in precision. Their confidence intervals vary in width, and some include zero while others lie above zero. A wider interval generally indicates that a broader range of effect sizes is compatible with the data under the analysis, while a narrower interval indicates greater statistical precision. These intervals should be interpreted alongside the distinct outcome definitions and time points, not as direct substitutes for the primary result.

Confidence intervals are also conditional on the analysis method and its assumptions. The registry identifies the primary method but does not report all implementation details, including any strata used. The interval is therefore best read as the uncertainty measure reported for the sponsor’s primary comparison, not as a complete account of every possible source of uncertainty.

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 are for participants per arm for the binary outcomes in this study. They are not totals across arms or event totals. The stated 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 set to the stated fraction of the observed effect. The original trial design assumptions and original sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a hypothetical design to have an 80% chance of detecting the selected effect under those assumptions, if that effect and assumptions are correct. The 90% power column gives the corresponding illustration for a 90% chance. These are planning probabilities for hypothetical repeated studies, not probabilities that the observed study result is true. This is not observed power.

Rows for 100% of the observed effect use the observed effect as the target; rows for 75% and 50% of the observed effect use progressively smaller targets. Smaller effects are harder to distinguish from random variation, so the illustrative requirement rises as the target effect gets smaller. The figures are sensitive to the assumed effect: the observed contrast may not be a reliable estimate of the effect a future study would encounter.

The illustrations should not be read as evidence that the trial was designed to those targets or that it achieved a particular power. They use the listed generic assumptions and the observed effect, whereas the registry record does not report the sponsor’s original design calculations.

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 = 0.346; treatment proportion p₁ = 0.495; average p̄ = 0.420.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6981 = 1.3683.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6901 = 0.5808.
4. n = (1.3683 + 0.5808)² / (0.1494)² = 170.2, rounded up to 171 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 <- 0.345794392523364                          # control proportion
p1 <- 0.495192307692308                          # 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(4294667)
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 = 171 (80% power), 228 (90% power)
 75% of observed effect: n per arm = 300 (80% power), 401 (90% power)
 50% of observed effect: n per arm = 664 (80% power), 889 (90% power)
power.prop.test: 170.2 
Simulated power at n = 171 per arm: 0.809 (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 sponsor’s primary analysis uses the Cochran-Mantel-Haenszel method and reports a difference in proportions of 14.6 percentage points, with a 95% confidence interval from 3.3 to 25.8 percentage points and p = 0.011. A separate simple recalculation from the posted summary counts is unadjusted and does not necessarily reproduce the sponsor’s method or any stratification incorporated in it.

The recalculated estimate and interval are close to the sponsor’s reported figures, and the registry record does not flag a discrepancy. The close agreement is a useful check that the broad numerical result is consistent with the posted summaries, but it does not make the two analyses methodologically identical. The sponsor’s analysis takes precedence as the reported trial analysis.

The registry does not provide enough detail to reconstruct every feature of the sponsor’s procedure. In particular, the strata and other implementation details are not reported in the registry record. The recalculation should consequently be understood as an independent, straightforward summary-data check, not as a correction or alternative primary analysis.

15. Multiplicity, Missing Data and Analysis Populations

Multiple testing is relevant because the registry lists numerous secondary outcomes, including different response definitions, disease activity measures, and assessment times. If many hypotheses are tested, the chance of at least one apparently strong result arising by chance can increase. Statistical approaches such as a prespecified hierarchy or an adjustment across comparisons can address this issue, but the registry record does not report whether such a strategy was planned or used. Accordingly, secondary p-values should be read cautiously and should not be treated as if each were the sole primary test.

The primary endpoint is clearly identified as BICLA response at Week 48, and the registry reports the sponsor’s analysis for it. However, the record summarized for this analysis does not provide a full statistical analysis plan, a detailed multiplicity procedure, or the original sample-size justification. It is not possible to infer these details from the observed results.

The Full Analysis Set includes randomized participants except 6 excluded because of persistent Good Clinical Practice non-compliance at the enrolling site. That exclusion is stated in the primary endpoint population definition. How missing Week 48 outcome data were handled, whether imputation was used, and how intercurrent events were addressed are not reported in the registry record. The impact of missing outcomes therefore cannot be evaluated from the posted summary alone.

The endpoint counts differ from the safety counts. This is not necessarily an inconsistency: efficacy and safety analyses can use different populations and denominators. The registry reports the primary endpoint analysis counts and separately reports participants at risk for adverse events. The reasons for all differences in analysis populations or exposure are not specified in the registry record.

These reporting gaps limit reconstruction and independent verification of the full analysis. They do not erase the reported primary result, but they mean that its interpretation should remain tied to the method and population explicitly described in the record.

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: systemic lupus erythematosus (1.4%), ophthalmic herpes zoster (0.9%), infusion related reaction (0.9%), lupus enteritis (0.9%), chest pain (0.9%).

The registry reports serious adverse events for 16 of 108 participants at risk in the placebo-plus-standard-of-care group and 21 of 213 participants at risk in the DZP-plus-standard-of-care group. It also reports other adverse events for 47 of 108 and 109 of 213 participants, respectively. These are counts with their reported safety denominators; they should not be compared using the efficacy analysis populations.

The registry lists one death in the DZP-plus-standard-of-care group and none in the placebo-plus-standard-of-care group. The record does not provide enough context in this summary to attribute the death to study treatment or to characterize its circumstances. The most frequently listed serious-event terms include systemic lupus erythematosus at 1.4%, ophthalmic herpes zoster at 0.9%, infusion related reaction at 0.9%, lupus enteritis at 0.9%, chest pain at 0.9%, and appendicitis at 0.9%.

These figures are descriptive. They do not by themselves establish whether an event was caused by treatment, and differences in counts should be interpreted in light of the distinct safety denominators and the absence of detailed exposure and event-context information in the registry record.

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

The registry’s primary result is a higher observed BICLA response percentage at Week 48 in the DZP-plus-standard-of-care group than in the placebo-plus-standard-of-care group. The sponsor reports a difference of 14.6 percentage points, with a 95% confidence interval from 3.3 to 25.8 percentage points and p = 0.011. This describes the comparison under the registry’s endpoint definition and analysis method.

The result does not mean that every participant receiving DZP met the response criteria, or that every participant in the comparator group failed to do so. The percentages are group summaries. They also do not identify which element of the composite endpoint drove the observed contrast, since BICLA requires simultaneous satisfaction of criteria involving BILAG 2004, SLEDAI-2K, and Physician’s Global Assessment.

A statistically detectable group difference is not, on its own, a judgment of clinical importance. The registry record does not provide a threshold for the smallest clinically important difference, nor does the primary result answer every question about durability, quality of life, or individual benefit and harm. The endpoint was assessed at Week 48, and the summary result should not be generalized to unreported time points or outcomes.

The result also does not prove that the same contrast will occur in every population or setting. It applies to this randomized study and its defined analysis population, with exclusions described for the Full Analysis Set. Details about missing-data handling and some analysis-plan elements are not reported in the registry record. The evidence should be interpreted with those limits in mind.

Finally, the primary comparison does not settle the interpretation of safety. Serious and other adverse events are reported descriptively with their own denominators, and the summary does not establish causality. Efficacy and safety evidence need to be considered as separate parts of the study record rather than inferred from one another.

18. Why This Trial Matters Statistically

Statistically, this trial is informative because it reports a randomized, placebo-controlled comparison of an add-on intervention against placebo on top of standard-of-care medication. Random allocation can support a fair comparison of groups, while masking can reduce some forms of bias in treatment delivery and outcome assessment. The registry identifies the study as randomized and quadruple-masked, though it does not specify which roles were masked in the record.

The primary outcome is a defined composite rather than a single laboratory value or symptom measure. That makes it important to understand the rules for response: a participant had to show BILAG improvement without worsening and also avoid worsening on SLEDAI-2K and Physician’s Global Assessment. This definition makes the result interpretable as a proportion meeting a complete clinical assessment rule, while also limiting what can be concluded about any one component.

The reported confidence interval gives more information than the point estimate alone by showing uncertainty around the estimated group difference. The sponsor’s primary interval lies above zero, and a simple unadjusted recalculation is close to the reported result. That agreement is reassuring as a numerical consistency check, while the sponsor’s named method remains the primary analysis.

The study also illustrates why secondary outcomes and multiplicity need careful handling. Several related outcomes can add context, but they do not all carry the same evidentiary status as a designated primary endpoint, especially when a multiplicity procedure is not reported. Likewise, hypothetical planning calculations based on observed effects are not a substitute for the original design rationale or evidence of achieved power.

Overall, the registry supports a focused statistical reading of the Week 48 primary comparison while leaving important questions about analysis details, missing data, and the broader secondary testing strategy unanswered.

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 limitations are specific to the information reported for this study. First, the primary outcome is a composite with multiple requirements. The overall response percentage does not show how much each BILAG, SLEDAI-2K, or Physician’s Global Assessment component contributed, and component-specific primary results are not reported in the registry record.

Second, the primary Full Analysis Set excludes 6 participants because of persistent Good Clinical Practice non-compliance at the enrolling site. The registry states this exclusion but does not provide further detail in the summary information. The effect of this exclusion on the comparison cannot be determined from the posted results alone.

Third, the summary record does not report how missing primary endpoint data were handled, whether imputation was used, or how events occurring after randomization were incorporated into the analysis. These details matter for interpreting a response endpoint assessed at Week 48. The full prespecified analysis plan and original sample-size rationale are also not reported in the registry record.

Fourth, the sponsor’s primary method is named as Cochran-Mantel-Haenszel, but the strata and implementation details are not reported in the information. A simple recalculation from group summaries cannot reproduce unreported features of that method. The sponsor’s result remains the primary reported comparison.

Finally, the record lists many secondary outcomes, but does not report a multiplicity strategy. The secondary results therefore offer context but should not be treated as a single confirmatory body of evidence. Safety figures are also descriptive, with safety denominators that differ from the primary endpoint population and without enough event context to establish attribution.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy and Safety of Dapirolizumab Pegol in Study Participants With Moderately to Severely Active Systemic Lupus Erythematosus — NCT04294667.
• Registry record last updated 2025-05-04; status last verified 2025-04.
• Results first posted 2025-04-24.
• 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

NCT04294667 is a completed Phase 3 randomized, quadruple-masked, parallel-group study of dapirolizumab pegol plus standard-of-care medication versus placebo plus standard of care in participants with moderately to severely active systemic lupus erythematosus. The registry lists 321 enrolled participants and records UCB Biopharma SRL as sponsor.

The primary endpoint was BICLA response at Week 48. The sponsor-reported difference in proportions was 14.6 percentage points, with a 95% confidence interval from 3.3 to 25.8 percentage points and p = 0.011. The record also reports secondary disease activity and response outcomes and descriptive adverse-event counts.

The registry does not report the original sample-size justification, full analysis plan, multiplicity strategy, or missing-data handling in the information summarized for this analysis. Those omissions limit independent reconstruction of the complete statistical approach.