A Study of Belimumab in Subjects With Systemic Lupus Erythematosus (SLE): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Belimumab in Subjects With Systemic Lupus Erythematosus (SLE) (NCT00424476), a randomized phase 3 study. The primary outcome is SLE Responder Index (SRI) Response Rate at Week 52.

2. Clinical Question

The clinical question is therefore about the proportion meeting a composite response definition, rather than change in a single symptom or measure. The result compares each belimumab dose with placebo. The registry record also lists safety, tolerability, and quality of life among the study aims, but the primary endpoint is the week 52 responder percentage.

3. Trial Design

This was a phase 3, randomized, double-blind, placebo-controlled, parallel-group study of belimumab in systemic lupus erythematosus. The official title describes a 52-week, multi-center study. The registry lists an enrollment of 865 and three groups: placebo, belimumab 1 mg/kg, and belimumab 10 mg/kg. The primary outcome analysis reports 287 participants in the placebo group, 288 in the 1 mg/kg group, and 290 in the 10 mg/kg group.

The study began in 2007-05, had primary completion in 2009-05, and is recorded as completed. The sponsor was Human Genome Sciences Inc. Participants received placebo or one of the two belimumab doses, with standard therapy described as background treatment in the brief summary. Specific details of standard therapy are not reported in the registry record.

Randomization is intended to make treatment groups comparable on average, while double blinding is intended to limit differences in care or assessment related to knowledge of assignment. These are general purposes of the design features, not evidence that every source of bias was eliminated. The registry record does not report allocation concealment details or the trial's original sample-size justification.

The primary endpoint was assessed at week 52. Several secondary outcomes were assessed at week 52 or week 24, including a SELENA SLEDAI improvement criterion, physician's global assessment, physical health-related quality of life, and prednisone reduction. The analysis population and missing-data handling described for the primary endpoint should not be assumed to apply to every secondary endpoint; those details are not reported in the registry record for the secondary outcomes.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was performed on a modified intention-to-treat (MITT) population, defined as all subjects who were randomized and received at least 1 dose of study agent. Subjects who required rescue SLE medications were declared nonresponders, as were subjects who dropped out or were missing Week 52 data.

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 SLE Responder Index (SRI) Response Rate at Week 52, measured over Baseline, 52 weeks.

The primary endpoint was the percentage of participants meeting the SLE Responder Index (SRI) definition at week 52. It combines three kinds of information: at least a 4 point reduction from baseline in SELENA SLEDAI, no worsening in Physician's Global Assessment (PGA), and no new BILAG A organ-domain score or two new BILAG B organ-domain scores compared with baseline.

SELENA SLEDAI summarizes disease activity using 24 descriptors. The record states that 0 indicates inactive disease, the theoretical maximum is 105, and scores greater than 20 are rare. PGA is a visual analog scale from 0 to 3, with the record describing 1 as mild, 2 as moderate, and 3 as severe. BILAG assigns a score for each of 8 organ domains, ranging from severe to no disease, represented by A to E.

A composite endpoint is used to require improvement on one measure while also limiting worsening on other measures. This can give a broader picture than a single component, but it also means the overall responder percentage depends on every part of the definition. A participant who improved on SELENA SLEDAI could still fail to meet the composite if the PGA or BILAG criteria were not met.

The registry record specifies that rescue SLE medication, dropout, or missing week 52 data led to classification as a nonresponder in the primary analysis. Thus, the reported response rate combines observed clinical criteria with those prespecified outcome classifications.

7. Results Posted in the Registry

• Belimumab 1 mg/kg: 51.4% (148/288) versus 43.6% (125/287) on control; risk difference 7.8 percentage points (95% CI -0.3 to 16.0), risk ratio 1.18 (0.99–1.40); unadjusted two-proportion z-test p = 0.060.
• Belimumab 10 mg/kg: 57.6% (167/290) versus 43.6% (125/287) on control; risk difference 14.0 percentage points (95% CI 6.0 to 22.1), risk ratio 1.32 (1.12–1.56); 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.

Percent of Subjects With a ≥ 4 Point Reduction From Baseline in SELENA SLEDAI Score at Wk 52.

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Belimumab 1 mg/kg: 53.1% (153/288) versus 46.0% (132/287) on control; risk difference 7.1 percentage points (95% CI -1.0 to 15.3), risk ratio 1.16 (0.98–1.36); unadjusted two-proportion z-test p = 0.087.
  • Belimumab 10 mg/kg: 58.3% (169/290) versus 46.0% (132/287) on control; risk difference 12.3 percentage points (95% CI 4.2 to 20.4), risk ratio 1.27 (1.08–1.49); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belimumab 1 mg/kg 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 higher for Belimumab 10 mg/kg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Mean Change in Physician's Global Assessment (PGA) at Wk 24.

• 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:
  • Belimumab 1 mg/kg: mean -0.44 versus -0.39 on control; difference -0.05 (95% CI -0.13 to 0.03), standardized effect d = -0.10; z-test p = 0.239.
  • Belimumab 10 mg/kg: mean -0.54 versus -0.39 on control; difference -0.15 (95% CI -0.23 to -0.07), standardized effect d = -0.29; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belimumab 1 mg/kg 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 lower for Belimumab 10 mg/kg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Mean Change From Baseline in Medical Outcomes 36-Item Short Form Health Survey (SF-36) Physical Component Summary Score (PCS) at Wk 24.

• 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:
  • Belimumab 1 mg/kg: mean 3.65 versus 3.64 on control; difference 0.01 (95% CI -1.17 to 1.19), standardized effect d = 0.00; z-test p = 0.987.
  • Belimumab 10 mg/kg: mean 3.58 versus 3.64 on control; difference -0.06 (95% CI -1.28 to 1.16), standardized effect d = -0.01; z-test p = 0.923.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belimumab 1 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Belimumab 10 mg/kg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover multiple aspects of disease activity, physician assessment, physical health-related quality of life, and prednisone reduction. Across this set, the overall pattern is mixed rather than uniformly aligned: some comparisons show greater improvement or response in a belimumab group, while other comparisons are close to placebo. This broader pattern is consistent with treating the primary SRI result as one endpoint among several, not as a summary of every clinical dimension examined.

The second SELENA SLEDAI response measure is related to the primary SRI because both involve a 4 point reduction, but it does not include all of the same requirements. The primary endpoint additionally incorporates PGA and BILAG worsening criteria. The secondary outcome pattern therefore provides related, but not interchangeable, evidence about response.

The registry reports four secondary outcomes in the summarized results. Their analyses include binary responder outcomes and continuous changes. The registry record does not report a multiplicity adjustment for these secondary comparisons. When many outcomes or comparisons are examined, the chance of at least one apparently notable result can increase. For that reason, unadjusted secondary p-values generally carry less confirmatory weight than a prespecified primary analysis with a clearly reported analysis plan.

Secondary outcomes can still help describe consistency, possible differences across domains, and questions for further study. They should be interpreted in context of their endpoint definitions, analysis populations, missing-data handling, and precision. For some secondary analyses, the available record does not report confidence intervals for the treatment contrast or detailed model specifications. Those omissions limit assessment of the size and uncertainty of the differences.

The secondary results do not overturn or independently validate the primary finding. They broaden the descriptive picture, while the absence of reported multiplicity procedures and some analysis details calls for caution when treating individual secondary comparisons as conclusive.

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

• Percent of Subjects With a ≥ 4 Point Reduction From Baseline in SELENA SLEDAI Score at Wk 52.
• Mean Change in Physician's Global Assessment (PGA) at Wk 24.
• Mean Change From Baseline in Medical Outcomes 36-Item Short Form Health Survey (SF-36) Physical Component Summary Score (PCS) at Wk 24.
• Percent of Subjects Whose Average Prednisone Dose Has Been Reduced by ≥ 25% From Baseline to ≤ 7.5 mg/Day During Weeks 40 Through 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: each participant is classified as meeting or not meeting the SRI response definition at week 52. A group response percentage is the proportion classified as responders. Comparing these proportions is one way to describe the observed treatment-group contrast.

What does a risk difference express?

General explanation: a risk difference subtracts the control-group event proportion from the intervention-group proportion. For a favorable outcome such as response, a positive difference indicates a higher observed response proportion in the intervention group. Its confidence interval describes a range of values compatible with the data and the calculation method. If the interval includes zero, the data are compatible with no difference under that method; if it excludes zero, they are less compatible with no difference. These are unadjusted recalculations from the posted summaries, not the sponsor's regression analysis.

What do odds ratios express?

General explanation: odds are the ratio of the probability of an event to the probability of no event. An odds ratio compares those odds between groups. It is not the same as a risk ratio, and it is not a percentage-point difference. The registry reports logistic-regression odds ratios for the primary outcome. The 10 mg/kg odds ratio is 1.83, with a 95% confidence interval from 1.30 to 2.59; the 1 mg/kg odds ratio is 1.55, with a 95% confidence interval from 1.10 to 2.19. Both sponsor-reported intervals are above 1, the reference value for equal odds.

The registry also reports p-values for these analyses. A p-value measures how unusual data at least as discrepant as those observed would be under a specified null model; it is not the probability that the null hypothesis is true, nor a measure of clinical importance. The sponsor-reported p-values are 0.001 for 10 mg/kg and 0.013 for 1 mg/kg. The registry record does not describe the full model specification or any covariates in the summarized results.

Why can the recalculations differ?

The recalculated risk differences use the posted group-level counts and are simple, unadjusted comparisons. The sponsor's results use logistic regression. A regression analysis may account for modeling choices or covariates that are not reflected in a direct comparison of proportions. The registry record does not report enough detail to identify the reason for the discrepancy. The sponsor's own analysis therefore takes precedence, while the unadjusted calculations serve as a separate descriptive check.

What does the modified intention-to-treat population mean?

The primary analysis included randomized participants who received at least one dose of study agent. This is the registry's stated modified intention-to-treat definition. It is narrower than a definition that includes every randomized participant, because it excludes randomized participants who received no dose. The registry also states that rescue SLE medication, dropout, and missing week 52 data were treated as nonresponse. This rule preserves a defined outcome classification for those cases, but it can affect the response percentage and does not reveal what their unobserved week 52 response would have been.

General explanation: missing-data rules matter because the outcome after dropout is unknown. Classifying missing outcomes as nonresponses is one possible approach, but its implications depend on why data are missing and on the scientific question. The registry record does not report sensitivity analyses for alternative assumptions about missing outcomes.

How should the secondary continuous outcomes be read?

The PGA and SF-36 outcomes are reported as mean changes from baseline, with standard errors. A mean change describes the average change in a group; a standard error describes uncertainty in the estimated mean, not the spread of individual participant values. The registry's reported analyses used ANCOVA for these outcomes. The recalculated mean differences are unadjusted comparisons based on posted summaries and do not replace the sponsor's analysis.

General explanation: ANCOVA can compare group outcomes while accounting for baseline values or other model terms, depending on the specification. The summarized registry results do not give the full model details. The registry record reports p-values for the comparisons, but does not provide confidence limits for the treatment contrasts for these continuous outcomes in the summarized results.

11. Confidence Intervals and Precision

Precision is conveyed by the range of values compatible with an estimate under its analysis method. A confidence interval is not a guarantee that the true effect lies within its endpoints; it expresses uncertainty in the estimate under the model and assumptions used. Wider intervals indicate less precision, while narrower intervals indicate greater precision.

For the sponsor's primary logistic-regression analysis, the 10 mg/kg odds ratio was 1.83, with a 95% confidence interval from 1.30 to 2.59. The 1 mg/kg odds ratio was 1.55, with a 95% confidence interval from 1.10 to 2.19. Both intervals are above the odds-ratio reference value of 1, though they also include a range of possible effect sizes. The registry record does not report confidence intervals for the sponsor's primary analysis on the risk-difference scale.

The unadjusted recalculations use another effect scale and another method. For the 1 mg/kg comparison, the recalculated risk-difference interval includes zero; for 10 mg/kg, it excludes zero. These intervals are not interchangeable with the sponsor's odds-ratio intervals. The discrepancy between analyses is important when interpreting apparent precision, and the sponsor's analysis takes precedence.

For secondary outcomes, the posted group means and standard errors indicate uncertainty around each mean, while the sponsor-reported ANCOVA p-values address model-based comparisons. The summarized record does not report confidence intervals for those treatment contrasts. A point estimate alone cannot show how precisely a contrast is estimated, and a p-value cannot replace a confidence interval as a description of plausible effect sizes.

Precision also concerns the endpoint definition and analysis population. The primary endpoint incorporates several disease measures and classifies rescue medication, dropout, or missing week 52 data as nonresponse. These choices define what the interval and estimate refer to; they do not remove uncertainty about alternative definitions or missing-data assumptions.

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 sample-size figures are planning illustrations based on the observed effects, not the original trial's design calculations. For these binary outcomes, the values mean participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect.

The 80% power column represents the number of participants per arm that the illustration estimates would be needed to detect the selected effect with 80% power under those assumptions. The 90% power column gives the corresponding planning number for 90% power. Power is the probability, under the assumed effect and model, of detecting that effect at the stated significance level. Higher target power generally requires more participants.

The rows for 100%, 75%, and 50% of the observed effect consider progressively smaller effects. Smaller effects require more participants to distinguish them from no difference with the same target power and assumptions. This relationship helps explain why planning estimates can rise sharply when a study is designed to detect a more modest effect.

These numbers are not observed power. They do not report the chance that this completed trial succeeded, and they do not revise the trial's original sample-size justification. The registry record does not report that original justification or its assumptions. The planning figures are hypothetical illustrations tied to the observed estimates; if the observed effect is imprecise or overestimated, planning directly from it may yield an overly optimistic target for a future study.

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 = 0.436; treatment proportion p₁ = 0.514; average p̄ = 0.475.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7062 = 1.3841.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7040 = 0.5925.
4. n = (1.3841 + 0.5925)² / (0.0783)² = 636.5, rounded up to 637 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 <- 0.435540069686411                          # control proportion
p1 <- 0.513888888888889                          # 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(424476)
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 = 637 (80% power), 852 (90% power)
 75% of observed effect: n per arm = 1,130 (80% power), 1,512 (90% power)
 50% of observed effect: n per arm = 2,536 (80% power), 3,394 (90% power)
power.prop.test: 636.5 
Simulated power at n = 637 per arm: 0.813 (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 posted recalculations are simple, unadjusted comparisons derived from the group summaries. The registry's own primary analyses instead report logistic-regression odds ratios for each belimumab dose versus placebo. Those sponsor-reported results are the authoritative analyses for interpreting the trial, because the recalculations do not reproduce the sponsor's model and the registry record flags a discrepancy.

For the primary endpoint, the sponsor reports an odds ratio of 1.83 for 10 mg/kg versus placebo, with a 95% confidence interval from 1.30 to 2.59 and p < 0.001. For 1 mg/kg versus placebo, the reported odds ratio is 1.55, with a 95% confidence interval from 1.10 to 2.19 and p = 0.013. These are odds ratios from logistic regression, not risk differences. They should be read alongside the arm response percentages to distinguish model-based relative odds from observed response proportions.

The secondary reported analyses also use logistic regression for the SELENA SLEDAI response outcome and ANCOVA for continuous outcomes. The available record does not describe all model details or explain why the sponsor results differ from the unadjusted calculations. The recalculations can provide a transparent descriptive cross-check, but they should not supersede the sponsor's analysis.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is described as modified intention-to-treat: participants had to be randomized and receive at least one dose of study agent. The registry further states that participants who required rescue SLE medication, dropped out, or lacked week 52 data were declared nonresponders for the primary endpoint. These rules are directly relevant to what the reported response percentages represent.

The summarized registry record does not report a multiplicity adjustment for the secondary outcomes, nor does it provide a complete hierarchy of hypotheses or a family-wise error strategy. With several endpoints and comparisons, unadjusted p-values should be treated as exploratory or supportive rather than as a set of independent confirmatory tests. The record lists six outcome measures and ten analyses, but the summarized information does not explain how those analyses were grouped for multiplicity control.

The missing-data rule for the primary endpoint is stated, but sensitivity analyses using different assumptions are not reported in the registry record. The reason for missing week 52 data and the pattern of missingness are also not reported in the summarized record. These details matter because a nonresponder classification may have different implications depending on why follow-up information was unavailable.

For secondary endpoints, the analysis population and approach to missing observations are not reported in the registry record. The trial's original sample-size justification, interim-analysis plan, and full statistical analysis plan are also not reported in the registry record. Without those details, it is not possible to assess from this summary whether all analyses followed a prespecified hierarchy or how deviations and missing outcomes were handled across endpoints.

These are limits on interpretation, not evidence that a particular analysis choice was inappropriate. They identify where the registry information does not allow an independent assessment of the trial's multiplicity and missing-data procedures.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (1.7%), pyrexia (1.4%), cellulitis (1.4%), urinary tract infection (1.4%), osteonecrosis (1.0%).

The registry lists serious adverse events for each study group as counts of affected participants among those at risk: 36 of 287 for placebo, 47 of 288 for belimumab 1 mg/kg, and 41 of 290 for belimumab 10 mg/kg. These are group-level safety summaries. They do not by themselves establish whether an event was caused by study treatment, and the record excerpt does not provide event timing, severity detail beyond the serious-event classification, or adjusted comparisons.

The posted adverse-event summary also gives counts for other adverse events: 222 of 287 in the placebo group, 219 of 288 in the 1 mg/kg group, and 223 of 290 in the 10 mg/kg group. The registry record summarized does not define the precise scope of this other-event category, so it should not be assumed to mean every event not classified as serious.

The most frequently listed serious-event terms include pneumonia at 1.7%, pyrexia at 1.4%, cellulitis at 1.4%, urinary tract infection at 1.4%, osteonecrosis at 1.0%, and lupus nephritis at 1.0%. The summarized information does not assign those listed percentages to a particular treatment group. Death counts are not reported in the registry record.

Safety counts need context, including duration of observation and event definitions. The reported figures describe what was recorded; they are not a causal comparison or medical recommendation.

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

The primary result describes the proportion of participants classified as SRI responders at week 52 under the registry's definition and missing-data rule. The posted percentages are higher in the belimumab groups than in the placebo group. The sponsor's logistic-regression analyses also report odds ratios above 1 for both dose comparisons, with confidence intervals above the reference value of 1. Because the unadjusted recalculations differ from the sponsor analyses, the sponsor's results take precedence.

This result does not mean that every participant in a belimumab group improved, or that the same outcome would occur for any particular person. The SRI is a composite: response requires improvement in one measure while avoiding specified worsening on other measures. Group averages and proportions cannot represent the full range of individual outcomes.

The endpoint does not capture every possible dimension of SLE, and a week 52 response result does not establish durability beyond the study period. It also does not answer all safety questions. Serious adverse-event counts are reported, but the summarized safety data do not provide a complete causal assessment or detailed comparisons of event timing and severity.

Interpretation depends on the modified intention-to-treat population and the rule that rescue medication, dropout, or missing week 52 data counted as nonresponse. The registry record does not report sensitivity analyses that show how alternative missing-data assumptions might affect the findings. The record also does not report the complete multiplicity plan for secondary outcomes, so those results warrant more caution than the primary analysis.

In short, the posted results show a higher observed week 52 response percentage in the belimumab groups, alongside sponsor-reported model-based comparisons. They do not establish that all outcomes favored treatment, that the observed differences apply to every patient, or that findings extend beyond the population and follow-up studied.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definition and analysis method matter in clinical biostatistics. The primary outcome is not a single measurement: it combines an improvement threshold on SELENA SLEDAI with restrictions on PGA and BILAG worsening. That composite may be more informative than any one component alone, but it also requires careful explanation of how each criterion contributes to classification.

The record also demonstrates that the same arm summaries can support different kinds of comparisons. The unadjusted recalculations express contrasts on a risk-difference scale, whereas the sponsor reports logistic-regression odds ratios. Those effect measures answer related but distinct questions. When results do not match exactly, the model and analysis population must be made explicit; a simple re-analysis should not be presented as if it were the trial's official inference.

Missing-outcome handling is another central design issue. The primary rule counts rescue medication, dropout, and missing week 52 data as nonresponse. This is transparent, but it makes the response definition partly dependent on follow-up and rescue-treatment events. Statistical interpretation should therefore identify the rule rather than describe the percentage as if every participant's outcome were directly observed.

Finally, multiple secondary outcomes create a need to distinguish confirmatory evidence from supportive patterns. The posted secondary findings span binary and continuous measures, and a consistent pattern across domains cannot be assumed. The absence of a reported multiplicity plan and some model details limits how strongly individual secondary p-values can be interpreted. Together, these features make the trial useful for understanding the relationship among estimand, endpoint, model, and uncertainty.

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 available record does not report the original sample-size justification, so the enrollment target cannot be evaluated against the trial's planned effect, power, or assumptions. The planning illustrations based on observed effects are not a substitute for that original rationale.

The registry summary does not give the full statistical analysis plan, complete logistic-regression model specification, covariates, or details sufficient to explain the discrepancy between sponsor analyses and unadjusted recalculations. The sponsor's own analyses take precedence, but the summarized record does not permit a full reconstruction of those models.

The primary analysis is modified intention-to-treat rather than an analysis of every randomized participant, because the stated population requires at least one dose. Missing week 52 data, dropout, and rescue medication are classified as nonresponse. The reasons for missingness, sensitivity analyses, and alternative missing-data evaluations are not reported in the registry record.

The record does not report a multiplicity adjustment for the secondary outcomes. Nor does the summarized information provide confidence intervals for all secondary treatment contrasts or complete analysis-population details for those outcomes. The number and breadth of outcomes make selective emphasis on isolated p-values especially difficult to assess.

Safety information is limited to the posted event counts and listed serious-event terms. Death counts are not reported in the registry record, and the summarized material does not describe event timing, exposure-adjusted rates, or detailed causal assessments. The study period is 52 weeks, so longer-term outcomes are not addressed by the primary follow-up.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Belimumab in Subjects With Systemic Lupus Erythematosus (SLE) — NCT00424476.
• Registry record last updated 2016-12-12; status last verified 2016-10.
• Results first posted 2011-05-05.
• 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

This completed phase 3 study compared placebo with belimumab 1 mg/kg and 10 mg/kg in participants with systemic lupus erythematosus over 52 weeks. It was randomized, double-blind, parallel-group, and described as multi-center. The primary endpoint was the week 52 SLE Responder Index response percentage.

The posted primary response percentages were 43.6% for placebo, 51.4% for belimumab 1 mg/kg, and 57.6% for belimumab 10 mg/kg. The registry's logistic-regression analyses reported odds ratios of 1.55 and 1.83 for the 1 mg/kg and 10 mg/kg comparisons, respectively. Because the unadjusted recalculations differ, the sponsor's analysis takes precedence.

The record describes rescue medication, dropout, and missing week 52 data as nonresponse in the primary analysis. Secondary outcomes span disease activity, physician assessment, physical health-related quality of life, and prednisone reduction. The registry record does not report the original sample-size justification or a multiplicity adjustment for the secondary outcomes.