A Study to Evaluate the Efficacy and Safety of Sifalimumab in Adults With 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 Sifalimumab in Adults With Systemic Lupus Erythematosus (NCT01283139), a randomized phase 2 study. The primary outcome is Percentage of Participants Achieving a Response in Systemic Lupus Erythematosus Responder Index 4 (SRI [4]).

2. Clinical Question

The SRI (4) definition combines changes across measures of disease activity and clinician assessment. It requires an improvement in SLEDAI-2K, without worsening on the Physician Global Assessment or BILAG-2004. This composite endpoint therefore asks whether response occurred across its specified components, rather than relying on one measure alone.

The registry reports response percentages for placebo and each of the three sifalimumab dose groups. The clinical question is not only whether the observed percentages differ, but also how uncertain those differences are and how the sponsor’s reported comparisons relate to simple recalculations from the group summaries. The trial also collected secondary outcomes and safety measures, though the registry record does not report results for every listed secondary outcome.

3. Trial Design

This was a randomized, double-masked, parallel-group phase 2 study of sifalimumab in adults with systemic lupus erythematosus. The registry describes the study as phase 2b and dose-ranging. It lists an enrollment of 834 and a completed status. The recorded study start was 2011-03-31, and primary completion was 2013-11-14.

Participants were assigned to placebo or one of three sifalimumab dose groups: 200 mg, 600 mg, or 1,200 mg. All regimens were intravenous and followed the same stated schedule: dosing every 2 weeks for 4 weeks, then monthly for 44 weeks, for a total of 14 doses. Placebo was described as matching sifalimumab. The registry identifies the allocation as randomized, the masking as double, and the model as parallel.

The primary endpoint was the percentage of participants achieving SRI (4) response at Day 365. Its stated analysis population was the modified intent-to-treat population, defined as randomized participants who received any investigational product and had a baseline primary efficacy measurement. The primary response groups contain 108 participants for placebo, 108 for sifalimumab 200 mg, 108 for sifalimumab 600 mg, and 107 for sifalimumab 1,200 mg.

The registry record does not report the original sample-size justification, the assumptions used to plan the trial, or whether interim analyses were planned or performed. Details of any additional stratification factors or allocation procedures are not reported in the registry record. Those omissions limit what can be inferred about the design decisions beyond the recorded randomized, double-masked, parallel structure.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: A total of 834 participants were screened out of which 402 participants did not meet eligibility criteria and were considered screen failures, and 432 participants were randomized into the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The modified intent-to-treat (mITT) population included all randomized participants who received any investigational product and had a baseline primary efficacy measurement.

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: Intent-to-treat (ITT) population included all participants who were randomized into the study.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving a Response in Systemic Lupus Erythematosus Responder Index 4 (SRI [4]), measured over Day 365.

The primary endpoint is the percentage of participants who met the SRI (4) responder definition at Day 365. It is a composite response: a participant must satisfy all stated components. First, SLEDAI-2K disease activity must fall by at least 4 points from baseline. Second, there must be no worsening in Physician Global Assessment, with worsening defined as an increase of at least 0.3 from baseline on a 0-3 visual analogue scale. Third, there must be no worsening on BILAG-2004, defined as at least 1 new ‘A’ score or 2 new ‘B’ scores compared with baseline.

A composite endpoint can capture response across several clinically assessed dimensions rather than treating a change in one measure as sufficient. In this trial, the definition requires improvement on SLEDAI-2K while also guarding against worsening on the other two specified measures. That makes the result a proportion meeting a joint rule, not a measure of the average change in any single scale.

The registry also notes that the increased DNA binding item of the SLEDAI-2K score was based on the ANA Multi-Lyte ANA-II Plus Test System. The primary response is reported as a percentage, with the analysis population restricted to randomized participants who received any investigational product and had a baseline primary efficacy measurement. The registry record does not report further details about how missing endpoint measurements were handled.

7. Results Posted in the Registry

• Sifalimumab 200 Milligram (mg): 58.3% (63/108) versus 45.4% (49/108) on control; risk difference 13.0 percentage points (95% CI -0.3 to 26.2), risk ratio 1.29 (0.99–1.67); unadjusted two-proportion z-test p = 0.057.
• Sifalimumab 600 mg: 56.5% (61/108) versus 45.4% (49/108) on control; risk difference 11.1 percentage points (95% CI -2.1 to 24.4), risk ratio 1.24 (0.96–1.62); unadjusted two-proportion z-test p = 0.102.
• Sifalimumab 1,200 mg: 59.8% (64/107) versus 45.4% (49/108) on control; risk difference 14.4 percentage points (95% CI 1.2 to 27.7), risk ratio 1.32 (1.02–1.71); unadjusted two-proportion z-test p = 0.034.

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.

Number of Participants With Abnormal Electrocardiogram (ECG) Findings Reported as TEAEs

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Sifalimumab 200 Milligram (mg): 0.0% (0/108) versus 1.9% (2/108) on control; risk difference -1.9 percentage points (95% CI -4.4 to 0.7); unadjusted two-proportion z-test p = 0.155.
  • Sifalimumab 600 mg: 0.9% (1/108) versus 1.9% (2/108) on control; risk difference -0.9 percentage points (95% CI -4.0 to 2.2), risk ratio 0.50 (0.05–5.43); unadjusted two-proportion z-test p = 0.561.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Sifalimumab 200 Milligram (mg) 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 Sifalimumab 600 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registered secondary outcomes span steroid reduction, skin disease activity, fatigue, adverse events, clinical laboratory findings, vital signs, and electrocardiogram findings. This set covers several dimensions beyond the primary composite response, including patient-reported symptoms, clinical measures, and safety monitoring. That breadth can provide context about the trial, but it does not make the secondary outcomes interchangeable with the primary endpoint.

The primary result concerns the SRI (4) response at Day 365. Secondary outcomes address other questions and may use different populations, timeframes, and definitions. A consistent pattern across well-reported secondary measures could add context to a primary result, while mixed or incomplete results would warrant more cautious interpretation. In this registry record, results are not reported for most of the listed secondary outcomes, so a broad pattern of secondary efficacy findings cannot be assessed.

Unadjusted secondary analyses generally carry less confirmatory weight when many outcomes and comparisons are considered. Testing many outcomes can increase the chance that some findings appear notable by chance. Whether the trial used any multiplicity adjustment or prespecified an order for secondary testing is not reported in the registry record. Secondary findings should therefore be treated as supporting or exploratory evidence unless their analysis plan and multiplicity handling are documented.

The registry does post a result for abnormal electrocardiogram findings reported as treatment-emergent adverse events, but the record does not provide reported analyses for the other secondary outcomes in the posted outcome list. No missing results should be inferred from the presence of an outcome definition alone. Overall, the secondary-outcome record is too incomplete to serve as a comprehensive cross-check of the primary efficacy comparison.

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

• Percentage of Participants on Greater Than or Equal to 10 mg/Day Oral Prednisone (or Equivalent) at Baseline Who Were Able to Reduce to Less Than or Equal to (<=) 7.5 mg/Day
• Percentage of Participants With a Cutaneous Lupus Erythematosus Disease Activity and Severity Index (CLASI) Activity Score Greater Than or Equal to (>=) 10 at Baseline Who Achieved a >= 4-point Reduction
• Percentage of Participants Who Achieved a Greater Than 3-Point Improvement in the Functional Assessment of Chronic Illness Therapy (FACIT)-Fatigue Scale
• Number of Participants With Treatment-Emergent Adverse Events (TEAEs) and Serious Adverse Events (TESAEs)
• Number of Participants With Abnormal Clinical Laboratory Parameters Reported as Treatment-Emergent Adverse Events (TEAEs)
• Number of Participants With Abnormal Vital Signs Reported as Treatment-Emergent Adverse Events (TEAEs)
• Number of Participants With Abnormal Electrocardiogram (ECG) Findings Reported as TEAEs

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary response, recorded as a percentage of participants meeting the SRI (4) definition. For this type of outcome, a group percentage summarizes the observed proportion of participants meeting the event definition. It is different from a continuous endpoint, such as a mean score, because it does not quantify how far above or below a threshold a participant’s measurement lies.

The sponsor’s reported method is logistic regression, with results expressed as odds ratios. Logistic regression is a standard method for relating a binary outcome to treatment group, and an odds ratio compares the odds of response between groups. Odds are not the same as probabilities or response percentages. An odds ratio above 1 indicates higher response odds in the numerator group relative to the comparison group, but it should not be read as an equal-sized percentage-point increase. The registry record does not report the full regression specification, including any covariates used.

The recalculated comparisons use unadjusted group summaries. A risk difference is the response proportion in one group minus the response proportion in the other group. It is an absolute contrast, expressed on the proportion scale. The recalculated risk differences are 0.130 for 200 mg, 0.111 for 600 mg, and 0.144 for 1,200 mg. These are simple unadjusted re-calculations from the posted summaries, not a replacement for the sponsor’s model-based analysis. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence.

A confidence interval describes a range of values compatible with the data under the method used, while reflecting sampling uncertainty. For an absolute difference, an interval that includes zero is compatible with no difference under that interval procedure; an interval entirely on one side of zero is less compatible with that possibility. For an odds ratio, the corresponding reference value is 1. The sponsor reports 90% confidence intervals for its odds ratios. The confidence level for the recalculated risk-difference intervals is not reported in the registry record.

A p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not describe the size or practical importance of a difference. The registry gives p-values for the sponsor’s logistic-regression comparisons and for the unadjusted recalculations. Because the approaches differ, those values should not be treated as interchangeable.

Allocation was randomized, which is intended to make treatment groups comparable on average, but randomization does not remove sampling uncertainty. The trial was double-masked, and placebo was described as matching the active treatment. The registry record does not report further details about masking procedures or the statistical methods used to preserve masking in the analysis.

The analysis population for the primary endpoint was modified intent-to-treat, not every person counted in the overall enrollment. It included randomized participants who received investigational product and had a baseline primary efficacy measurement. The registry record does not report the number excluded from this population, the reasons for exclusion, or the handling of missing Day 365 measurements. It also does not report imputation procedures or sensitivity analyses for missing data.

There are several dose-versus-placebo comparisons and multiple outcomes. Multiplicity refers to the increased chance of at least one apparently unusual result when many statistical comparisons are made. Adjustment methods can alter how evidence is interpreted across a family of tests. Whether any such adjustment was planned or used is not reported in the registry record. Thus, individual p-values should be understood in the context of several reported comparisons, rather than as if each were the sole test in the study.

For binary outcomes, the variance depends on the underlying event probability. General statistical note: if outcomes are more variable than a model assumes, standard errors may be too small and intervals too narrow unless the analysis accounts for that extra variation. The registry record does not report an over-dispersion concern for this binary endpoint, and the primary analysis is described as logistic regression. Over-dispersion is more commonly a concern in particular count-data models; it should not be presumed simply because an endpoint is clinical.

11. Confidence Intervals and Precision

The group percentages provide the observed response levels, while intervals and model-based results indicate how much uncertainty accompanies comparisons. The recalculated risk-difference intervals include zero for sifalimumab 200 mg and 600 mg versus placebo, but not for 1,200 mg versus placebo. This pattern means that, under the recalculation method, the first two intervals include no absolute difference, while the third lies on the positive side of zero. The confidence level for these recalculated intervals is not reported in the registry record.

The sponsor’s odds-ratio estimates have reported 90% confidence intervals: 1.03 to 2.71 for 200 mg, 1.01 to 2.54 for 600 mg, and 1.16 to 2.94 for 1,200 mg. Each interval lies above the odds-ratio reference value of 1. The sponsor’s intervals and the recalculated risk-difference intervals are based on different effect measures and analysis approaches, so their boundaries should not be compared as if they were the same quantity.

Intervals express precision, not certainty that a particular value is true. Wider intervals indicate greater uncertainty about the size of an effect; narrower intervals indicate more precision under the stated method. Even when an interval excludes its null reference value, it does not establish that the estimated effect is clinically important or that the same result would occur in another setting. The registry record does not report intervals around the individual response percentages themselves.

The reported primary group sizes are 108 in placebo, 108 in the 200 mg group, 108 in the 600 mg group, and 107 in the 1,200 mg group. The enrollment count of 834 refers to the study record, whereas these denominators describe the primary efficacy groups. The registry does not give a complete account of the path from overall enrollment to the modified intent-to-treat analysis population or explain the absence of the other enrolled participants from these primary denominators.

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 per arm, not totals across both arms. They use the observed effect as a starting point and show alternative planning scenarios for detecting the full observed effect, 75% of it, or 50% of it. Each row pairs a target effect with a planned number of participants per arm for 80% power and for 90% power. The figures are planning illustrations, not the trial’s original design justification.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The record’s sample-size assumption description specifies that non-time-to-event illustrations give participants per arm; this primary endpoint is a binary percentage outcome. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

In plain language, 80% power is the design target for a study that would detect the specified effect under the planning assumptions in 80% of repetitions of the assumed study process. The 90% power column uses a higher detection target under those same assumptions. Higher target power generally requires more participants for a given effect. Likewise, smaller effects require more participants to detect than larger effects when other assumptions are held fixed. The displayed numbers are not observed power; they are planning illustrations based on the observed effect and the stated assumptions.

The planning counts should not be read as evidence that the completed trial had those numbers in each group, nor as a retrospective measure of how successful the trial was. They illustrate how required group size changes with the effect size being targeted and the chosen power target. They do not account for any design features or analysis adjustments not listed in the planning assumptions.

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 = 0.454; treatment proportion p₁ = 0.583; average p̄ = 0.519.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7066 = 1.3850.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7007 = 0.5897.
4. n = (1.3850 + 0.5897)² / (0.1296)² = 232.0, rounded up to 233 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 <- 0.453703703703704                          # control proportion
p1 <- 0.583333333333333                          # 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(1283139)
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 = 233 (80% power), 311 (90% power)
 75% of observed effect: n per arm = 414 (80% power), 554 (90% power)
 50% of observed effect: n per arm = 933 (80% power), 1,248 (90% power)
power.prop.test: 232 
Simulated power at n = 233 per arm: 0.793 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses using logistic regression, with odds ratios and 90% confidence intervals. The reported odds ratios are 1.71 for sifalimumab 200 mg, 1.60 for 600 mg, and 1.84 for 1,200 mg, each compared with placebo. The corresponding reported p-values are 0.057, 0.094, and 0.031.

The separate recalculations use the posted response summaries to estimate unadjusted risk differences. This is a different effect measure and a different analysis approach from the sponsor’s logistic-regression odds ratios. A risk difference expresses an absolute contrast in proportions; an odds ratio compares odds. Even when both analyses use the same treatment groups, their estimates and p-values need not be identical.

The record flags a discrepancy between the posted summary-based recalculations and the sponsor’s analysis. For that reason, the sponsor’s own analysis takes precedence as the trial’s reported inferential analysis. The recalculations remain useful as a transparent, unadjusted comparison of the posted group summaries, but they should not be presented as the sponsor’s result or as a correction to it. The registry record does not provide enough detail to identify every source of the discrepancy.

The sponsor’s analysis does not by itself answer whether multiplicity was addressed. The registry record does not report whether the dose comparisons were adjusted for the number of comparisons or whether a hierarchy among doses was prespecified. The reported estimates and intervals should therefore be interpreted alongside that documentation gap.

15. Multiplicity, Missing Data and Analysis Populations

Several features make multiplicity relevant: the primary endpoint is compared across three sifalimumab dose groups against placebo, and the registry lists multiple secondary outcomes. The record reports 9 outcome measures and 15 analyses. When many comparisons are made, the probability of at least one apparently unusual result can rise even if there is no underlying treatment difference for any comparison. This is a general statistical issue, not evidence that a particular finding is false.

The registry record does not report whether the primary dose comparisons were adjusted for multiplicity, whether a dose-selection hierarchy was used, or whether secondary outcomes were tested under a prespecified sequence. It does not report a family-wise error strategy or other multiplicity procedure. Consequently, the individual reported p-values cannot be interpreted as if the set of comparisons had necessarily been accounted for as a whole.

The record identifies the primary analysis population as modified intent-to-treat: randomized participants who received any investigational product and had a baseline primary efficacy measurement. It does not report the number of randomized participants omitted from that population, the reasons for omission, or the number with missing primary endpoint measurements. The method for handling missing data, including any imputation, censoring, or sensitivity analysis, is not reported in the registry record.

The sample-size assumptions used in the original trial design are also not reported in the registry record. Planning illustrations based on the observed effect are not a substitute for that original justification. Interim analyses, stopping rules, the full statistical analysis plan, and details of any prespecified subgroup analyses are not reported in the registry record. These omissions limit assessment of whether the posted analyses match a prespecified plan and how missingness or multiple testing may affect interpretation.

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 2% 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 (6.5%), anaemia (1.9%), pneumonia (1.9%), acute myocardial infarction (1.9%), pyelonephritis acute (1.9%).

The registry reports serious adverse event counts among 108 participants in placebo, 108 in sifalimumab 200 mg, 108 in sifalimumab 600 mg, and 107 in sifalimumab 1,200 mg. The corresponding numbers with serious adverse events were 19, 16, 22, and 21. These are event-affected participant counts as reported for the groups; they are not measures of the primary efficacy outcome.

The record lists systemic lupus erythematosus as a serious adverse event term at 6.5%. Other listed serious terms are anaemia, pneumonia, acute myocardial infarction, acute pyelonephritis, and septic shock, each at 1.9%. These terms describe events reported in the registry, but the registry record does not give a complete treatment-group breakdown for each term. A term’s appearance does not establish that treatment caused it.

Deaths are not reported in the registry record. The serious-event counts should be read alongside the group denominators and the duration of observation, rather than as a direct comparison of treatment risk without further analysis. The registry record does not provide a detailed adjusted safety comparison or enough information to establish causal attribution for individual events.

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

The posted primary results show that the reported Day 365 SRI (4) response percentages were higher in each sifalimumab dose group than in the placebo group. The sponsor’s logistic-regression comparisons also report odds ratios above 1 for each dose. These are descriptions of the registry’s observed results and reported analyses; they are not, by themselves, a complete statement about the size, certainty, or clinical importance of any difference.

The estimates are uncertain, and the sponsor analysis differs from the unadjusted recalculations. The sponsor’s reported analysis takes precedence for the trial’s inferential findings. The recalculated risk-difference intervals have different patterns across doses, but those intervals arise from a simple unadjusted approach and should not be substituted for the sponsor’s model-based comparisons. Multiplicity adjustment is not reported, so the individual comparisons should not be treated as a fully documented family of confirmatory tests.

The SRI (4) endpoint is a defined composite response, not a direct measure of every aspect of SLE or of a participant’s experience. The result does not establish the effect on secondary outcomes for which results are not reported in the registry record. Nor do the group-level response percentages explain which component of the composite was most influential for individual participants.

These registry results do not establish what would occur in other populations, over other periods, or under different treatment schedules. They do not establish causation for individual adverse events, and they do not replace a full appraisal of the analysis plan, missing data, or the complete safety record. No treatment recommendation follows from these statistical summaries.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares three doses with a shared placebo group and reports both group response percentages and sponsor model-based comparisons. The dose-ranging structure makes it possible to examine whether the observed response pattern is similar across doses, while also raising the importance of understanding how multiple comparisons were handled.

It also illustrates why the analysis scale matters. A risk difference describes an absolute contrast in response proportions; an odds ratio describes a relative contrast in odds. Both can be useful, but they are not interchangeable. The recalculated unadjusted results and the sponsor’s logistic-regression results therefore need to be presented as distinct analyses, with the sponsor’s own analysis taking precedence when a discrepancy is flagged.

The endpoint itself reinforces a further statistical point: a composite response requires several conditions to be met. Its interpretation depends on the defined components and thresholds, not merely on the headline response percentage. Readers need the endpoint definition, analysis population, and time point to understand what the reported percentage represents.

Finally, the record distinguishes trial enrollment from the smaller denominators used in the primary efficacy groups, but does not explain the full flow into the modified intent-to-treat population. It also lacks detail on multiplicity and missing-data handling. Those gaps show why a numerical result is best interpreted together with the analysis plan and participant accounting, not in isolation.

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 registry record for this trial. The primary efficacy result is available for the modified intent-to-treat groups, but the registry does not explain the full transition from the enrollment of 834 to the primary group denominators of 108, 108, 108, and 107. Reasons for exclusions and the handling of missing Day 365 measurements are not reported in the registry record.

The sponsor’s analysis is reported as logistic regression, but the full model specification is not reported. The registry does not identify the covariates, if any, used in the model, or explain the discrepancy with the simple unadjusted recalculations. This restricts independent reconstruction of the sponsor’s estimates. The sponsor’s own analysis remains the primary reported inferential result when the discrepancy is present.

The registry record does not report multiplicity handling for the three dose comparisons or the broader set of outcomes. It also does not report the original sample-size justification, interim-analysis plans, stopping rules, or a complete statistical analysis plan. These omissions prevent a full assessment of prespecification and of how the reported p-values relate to the complete testing strategy.

Many secondary outcomes are listed without posted results. The safety information includes serious adverse event counts and selected serious-event terms, but does not provide a complete account of treatment attribution or all event details in the registry record. These limitations mean that efficacy and safety interpretation should remain tied to the information actually reported, rather than filling gaps with assumptions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy and Safety of Sifalimumab in Adults With Systemic Lupus Erythematosus — NCT01283139.
• Registry record last updated 2018-04-19; status last verified 2018-03.
• Results first posted 2016-07-11.
• 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

NCT01283139 is a completed randomized, double-masked, parallel phase 2 study of sifalimumab in adults with systemic lupus erythematosus. It enrolled 834 participants and compared intravenous sifalimumab at 200 mg, 600 mg, and 1,200 mg with matching placebo. The primary endpoint was SRI (4) response at Day 365 in a modified intent-to-treat population.

Reported response percentages were 45.4% for placebo and 58.3%, 56.5%, and 59.8% for the three sifalimumab doses, respectively. The sponsor reported logistic-regression odds ratios and 90% confidence intervals. Unadjusted recalculations differ in method; with a discrepancy flagged, the sponsor’s own analysis takes precedence. The registry record does not report multiplicity handling, missing-data methods, or the original sample-size justification. It also lists secondary outcomes for which results are not reported in the registry record.