Subcutaneous Treatment In Randomized Subjects To Evaluate Safety And Efficacy In Generalized Lupus Erythematosus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Subcutaneous Treatment In Randomized Subjects To Evaluate Safety And Efficacy In Generalized Lupus Erythematosus (NCT01405196), a randomized phase 2 study. The primary outcome is Percentage of Participants Achieving Systemic Lupus Erythematosus (SLE) Responder Index (SRI) at Week 24.

2. Clinical Question

3. Trial Design

The registry describes a randomized, double-blind, placebo-controlled, multicenter, dose-ranging Phase 2 study of PF-04236921 in systemic lupus erythematosus. The allocation model was parallel, and masking was recorded as quadruple. The study title identifies the treatment as subcutaneous. Enrollment was 183. The record gives a start date of 2011-12, a primary completion date of 2014-03, and a completed status.

Four dose or comparator groups are described: PF-04236921 10 mg, PF-04236921 50 mg, PF-04236921 200 mg, and placebo. The primary Week 24 outcome includes reported results for 10 mg, 50 mg, and placebo. The registry states that sponsor decision led to premature termination of dosing in the 200 mg arm, which was consequently excluded from the primary endpoint analysis. The safety results include the 200 mg group, so the analyzed groups are not identical across outcome types.

The registry defines the Full Analysis Set as all randomized participants who received at least 1 dose of study drug. For the primary outcome, it says the number analyzed was participants who completed through the Week 24 visit. The record does not give the original allocation target, the planned dose schedule, or the sponsor’s original sample-size justification. Interim-analysis plans and stopping rules beyond the statement about the 200 mg arm are not reported in the registry record.

The study objective was to compare three PF-04236921 dose levels with placebo using the SLE Responder Index, alongside secondary and exploratory measures. The primary outcome is a percentage, so it describes the proportion of analyzed participants meeting a defined response rule. It does not describe the size of an average change on a continuous scale.

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: Due to safety reason, dosing in 200 mg reporting arm was prematurely terminated and the participants were discontinued from it. Therefore, the statistical analysis plan was amended after it and 200 mg reporting arm was not included in efficacy data analysis.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set= all randomized participants who received at least 1 dose of study drug. Number of participants analyzed= participants who completed through the Week 24 visit. As per sponsor's decision, dosing in "PF-04236921 200 mg" arm was prematurely terminated and hence it was not included in efficacy analysis.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving Systemic Lupus Erythematosus (SLE) Responder Index (SRI) at Week 24, measured over Week 24.

The primary endpoint was the percentage of participants achieving the Systemic Lupus Erythematosus Responder Index at Week 24. The SRI combines disease-activity information from the SLEDAI-2K, BILAG 2004, and the Physician’s Global Assessment. Under the registry definition, a participant had to avoid treatment failure and meet all of the response criteria: at least a 4-point reduction in SLEDAI-2K, no new BILAG A organ-domain score or 2 new BILAG B organ-domain scores, and no worsening in PhGA of 0.3 points or more.

The registry describes treatment failure as including new or increased use of corticosteroids, immunosuppressants, or antimalarial drugs; death; hospitalization or treatment discontinuation due to SLE; or a lupus flare interfering with study participation. SLEDAI-2K assesses disease activity, with higher scores indicating greater severity. BILAG assesses disease extent and severity, while PhGA assesses worsening in general health status.

Composite responder outcomes are used to require improvement across several clinically relevant dimensions rather than relying on one measure alone. That design also means the response rate depends on every component and the treatment-failure rule. The endpoint therefore represents the proportion meeting the complete definition, not the proportion meeting any one component. The registry record does not report a separate rationale for choosing this endpoint.

7. Results Posted in the Registry

• PF-04236921 10 Milligram (10 mg): 60.0% (21/35) versus 40.5% (17/42) on control; risk difference 19.5 percentage points (95% CI -2.5 to 41.5), risk ratio 1.48 (0.94–2.34); unadjusted two-proportion z-test p = 0.088.
• PF-04236921 50 mg: 38.9% (14/36) versus 40.5% (17/42) on control; risk difference -1.6 percentage points (95% CI -23.4 to 20.2), risk ratio 0.96 (0.55–1.66); unadjusted two-proportion z-test p = 0.886.

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.

Patient Global Visual Analog Scale (VAS) Scores at Baseline

• 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:
  • PF-04236921 10 Milligram (10 mg): mean 50.44 versus 49.47 on control; difference 0.97 (95% CI -7.67 to 9.61), standardized effect d = 0.05; z-test p = 0.826.
  • PF-04236921 50 mg: mean 47.70 versus 49.47 on control; difference -1.77 (95% CI -10.43 to 6.89), standardized effect d = -0.08; z-test p = 0.689.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PF-04236921 10 Milligram (10 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 PF-04236921 50 mg and the control. The interval gives the range of effects that remain compatible with the data.

Functional Assessment of Chronic Illness Therapy - Fatigue (FACIT-F) Score at Baseline

• 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 deviations.
• Result:
  • PF-04236921 10 Milligram (10 mg): mean 25.91 versus 25.96 on control; difference -0.05 (95% CI -0.76 to 0.66), standardized effect d = -0.03; z-test p = 0.891.
  • PF-04236921 50 mg: mean 29.38 versus 25.96 on control; difference 3.42 (95% CI 2.75 to 4.09), standardized effect d = 2.09; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between PF-04236921 10 Milligram (10 mg) and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for PF-04236921 50 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes covering SRI response at earlier visits, a modified SRI through Week 24, BICLA response, SRI components, laboratory results, discontinuations due to adverse events, and treatment-emergent adverse events, including infectious events. This range includes additional efficacy measures as well as safety measures. It offers context around the primary composite endpoint, but the different outcomes do not all measure the same construct or use the same analysis population.

The detailed secondary results represented in the posted information also include baseline Patient Global VAS and FACIT-F measurements. Baseline values describe participants before the outcome period; they are not treatment-effect estimates. A difference in baseline means cannot establish a post-treatment difference. The record lists 23 secondary outcomes, but the outcome-level information summarized for interpretation does not establish a complete pattern of treatment effects across all those outcomes. Claims about consistency across the full set are therefore not warranted.

Secondary outcomes can help explain whether findings on the primary endpoint align with other measures, but they do not automatically confirm or overturn the primary result. SRI, modified SRI, and BICLA have distinct definitions, and their response rules can classify participants differently. Safety outcomes answer different questions again. The 200 mg arm’s exclusion from the primary efficacy analysis also limits direct comparisons across the efficacy and safety summaries.

In general, interpreting many outcomes creates a multiplicity problem: when numerous hypotheses are tested, the chance of at least one apparently notable result arising by chance can increase. Unadjusted secondary results therefore carry less weight than a prespecified primary analysis unless the analysis plan and multiplicity strategy support stronger confirmatory interpretation. The registry record does not report such a strategy. Secondary findings should be treated as supportive or exploratory unless their status and analysis are established in the record.

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

• Percentage of Participants Achieving Systemic Lupus Erythematosus (SLE) Responder Index (SRI) at Week 4, 8, 12, 16, and 20
• Percentage of Participants Achieving Modified Systemic Lupus Erythematosus (SLE) Responder Index (SRI) at Week 4, 8, 12, 16, 20, and 24
• Percentage of Participants Achieving British Isles Lupus Assessment Group-based Composite Lupus Assessment (BICLA) Response at Week 4, 8, 12, 16, 20, and 24
• Percentage of Participants Achieving Pre-defined Criteria for Systemic Lupus Erythematosus (SLE) Responder Index (SRI) Components at Week 24
• Number of Participants With Clinically Significant Laboratory Tests Results
• Number of Participants Who Discontinued Due to Adverse Events
• Number of Participants With Treatment-Emergent Adverse Events (AEs) or Serious Adverse Events (SAEs)
• Number of Participants With Treatment-Emergent Infectious Adverse Events (AEs) or Serious Adverse Events (SAEs)

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary outcome such as achieving or not achieving the SRI, the observed percentage is a proportion of participants classified as responders. Comparing two such proportions can be expressed in several ways. A risk difference subtracts the comparator proportion from the intervention proportion; an odds ratio compares the odds of response between groups. These measures answer related but different questions and use different numerical scales. A risk difference of zero represents equal observed proportions, while an odds ratio of one represents equal odds. Those reference values should not be treated as identical quantities.

The posted recalculations are unadjusted comparisons based on the displayed summary counts. The 10 mg comparison uses 21 responders among 35 analyzed participants and 17 among 42 in placebo. The 50 mg comparison uses 14 among 36 and the same placebo count of 17 among 42. The recalculated risk differences are 0.195 and -0.016, respectively. The associated intervals and unadjusted p-values quantify uncertainty for those simple comparisons. They do not account for any covariates or other modeling choices unless stated, and no such adjustments are part of these recalculations.

The registry’s sponsor results use mixed models and report odds ratios. The 10 mg sponsor estimate is 2.23 with a 90% confidence interval of 0.89 to 5.62 and p = 0.076; the 50 mg estimate is 0.96 with a 90% confidence interval of 0.38 to 2.41 and p = 0.528. The model-based estimates should be interpreted as sponsor analyses, not as the unadjusted risk-difference calculations. The record does not give enough detail to reconstruct the mixed-model specification, covariates, or handling of repeated measures. Because the discrepancy flag is true, the sponsor’s own analysis takes precedence over the recalculation.

In general, a confidence interval expresses uncertainty about an estimate under the assumptions of the analysis. An interval that includes the null value does not prove that there is no effect; it indicates that the data and method do not isolate the estimate from that null at the interval’s stated level. A p-value measures how surprising the data would be under a specified null model. It is not the probability that the null hypothesis is true, nor does it quantify the probability that a result will replicate.

The planned primary endpoint is a composite binary response. A participant is classified as either meeting the complete SRI definition or not meeting it. That classification discards information about how close a nonresponder came to the criteria and how much change occurred within each component. It also means that participants may fail to qualify for different reasons. The response percentage therefore summarizes the complete rule rather than identifying which component drove a result.

The registry’s population description distinguishes the Full Analysis Set from the number analyzed for the primary outcome. The Full Analysis Set includes randomized participants who received at least 1 dose. The endpoint description says the analyzed participants completed through Week 24. The record does not explain how participants without a Week 24 completion were handled, whether imputation was used, or whether additional analysis populations were assessed. Those details matter because excluding participants with incomplete follow-up can affect the interpretation of a proportion.

The number of enrolled participants is not a substitute for the denominator in a particular outcome analysis. The primary endpoint results use the listed outcome-specific group counts, and safety outcomes use their own at-risk counts. The 200 mg group appears in the safety reporting but not in the primary response comparisons. It would be inappropriate to infer that all outcome analyses used the same participants or analysis rules.

General statistical note: the precision of a proportion depends on the number of observations and on how common the outcome is, while the precision of a treatment contrast depends on both groups. Small groups can leave a broad range of plausible effects even when the observed percentages differ. A wide interval should be read as uncertainty, not as evidence that the true effect must be large. Conversely, a narrow interval is not proof that the analysis was free from bias or that its assumptions were correct.

The registry record reports multiple secondary outcomes and many analyses, but it does not provide a statistical-analysis plan in the information summarized for these results. The record does not report the planned model details for the secondary endpoints, multiplicity adjustments, or a hierarchy governing which comparisons were confirmatory. Therefore, an unadjusted secondary p-value should not be interpreted as if it were an isolated primary test with no other analyses.

11. Confidence Intervals and Precision

The unadjusted risk-difference estimate for 10 mg versus placebo is 0.195, with an interval from -0.025 to 0.415. The estimate for 50 mg versus placebo is -0.016, with an interval from -0.234 to 0.202. Both intervals include zero and extend to values on either side of it. In general, this indicates that the observed estimates are not precise enough to rule out effects in either direction under the recalculated method. The interval limits should be read alongside the point estimate, not as a range in which the true effect is guaranteed to lie.

The sponsor’s model-based estimates also have broad intervals relative to their point estimates. For 10 mg, the sponsor reports an odds ratio of 2.23 with a 90% confidence interval from 0.89 to 5.62. For 50 mg, the reported odds ratio is 0.96 with a 90% confidence interval from 0.38 to 2.41. Both sponsor intervals include the odds-ratio null value of one. These are 90% intervals from the sponsor analysis and are distinct from the recalculated risk-difference intervals.

In general, a confidence interval communicates the uncertainty associated with an estimate under a specified analysis. Its width is affected by the amount and distribution of information and by the method used. It does not capture every source of uncertainty, such as limitations in outcome measurement, missing-data handling, or model selection. Here, the record does not report enough detail to assess all such sources.

The group sizes listed for the primary comparisons are modest, and the intervals leave substantial uncertainty around the treatment contrasts. A single point estimate should not be treated as a definitive summary of the range of effects compatible with the data. Nor does the interval by itself establish clinical importance, which requires interpretation of the endpoint and its context.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial’s original design assumptions. The record’s planning method uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers detecting the stated fraction of the observed effect. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

For the binary primary outcome, the displayed figures are participants per arm. The 80% power column describes the planned group size that would give an 80% chance of detecting the specified effect under the listed assumptions if that effect were the true one. The 90% power column uses a higher target chance of detection and therefore generally requires a larger group size. These are planning concepts, not guarantees about the result of a particular study.

The rows describe planning for the full observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller effects require more participants to distinguish them from random variation under the same assumptions. This is why the planning figures increase as the target effect is reduced. The illustration uses the observed effect as its starting point, so it should not be mistaken for an independent estimate of the effect likely to occur in another study.

These figures are not observed power. Observed power is not a useful substitute for reading the estimate, interval, and data directly. The planning numbers instead show how sensitive a future design’s size would be to the effect it aims to detect and the desired probability of detecting it.

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 = 0.405; treatment proportion p₁ = 0.600; average p̄ = 0.502.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7071 = 1.3859.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6935 = 0.5837.
4. n = (1.3859 + 0.5837)² / (0.1952)² = 101.8, rounded up to 102 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 <- 0.404761904761905                          # control proportion
p1 <- 0.6                          # 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(1405196)
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 = 102 (80% power), 136 (90% power)
 75% of observed effect: n per arm = 182 (80% power), 243 (90% power)
 50% of observed effect: n per arm = 408 (80% power), 545 (90% power)
power.prop.test: 101.8 
Simulated power at n = 102 per arm: 0.819 (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 reported primary analyses compare PF-04236921 with placebo using mixed models and odds ratios. For 10 mg, the estimate is 2.23, with a 90% confidence interval from 0.89 to 5.62 and p = 0.076. For 50 mg, the estimate is 0.96, with a 90% confidence interval from 0.38 to 2.41 and p = 0.528. These values are the sponsor’s own analyses as recorded in the registry.

The recalculations instead use unadjusted risk differences from the posted response counts. For 10 mg the risk difference is 0.195, with an interval from -0.025 to 0.415 and p = 0.088; for 50 mg it is -0.016, with an interval from -0.234 to 0.202 and p = 0.886. An odds ratio and a risk difference use different scales, and the mixed-model method may also differ from a simple comparison of proportions. Their estimates and p-values are therefore not expected to be identical.

The registry flags a discrepancy between the posted sponsor analysis and recalculation. For that reason, the sponsor’s own analysis takes precedence when describing the registry’s inferential result. The recalculation is useful as a transparent, unadjusted check of the summary counts, but it is not a replacement for the sponsor’s method. The record does not report sufficient model details to reproduce the sponsor analysis independently.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome: the percentage achieving SRI at Week 24. It also lists numerous secondary measures and a large number of analyses. The statistical-analysis plan, including the planned hierarchy of tests and any adjustment for multiple comparisons, is not reported in the registry record. Without that information, it is not possible to determine which secondary comparisons were intended to be confirmatory or whether the sponsor controlled the overall false-positive rate across the analysis program.

In general, testing many outcomes, doses, and time points creates more opportunities for chance findings. Multiplicity procedures can change how evidence is evaluated across a family of tests. An unadjusted p-value answers a narrower question than a multiplicity-adjusted analysis and should not be treated as if no other tests were conducted. The sponsor’s primary model results are reported, but the record does not provide enough detail to reconstruct all analytical decisions.

The registry describes the Full Analysis Set as randomized participants who received at least 1 dose. For the primary endpoint, the analyzed participants are described as those who completed through the Week 24 visit. The record does not report the number excluded from that analysis, reasons for noncompletion, the handling of missing Week 24 outcomes, or whether sensitivity analyses assessed alternative assumptions. These omissions limit assessment of how missing data might affect the response percentages.

The record also does not report the sponsor’s original sample-size assumptions, interim-analysis plan, or detailed stopping rules. It does state that dosing in the 200 mg arm was prematurely terminated by sponsor decision, and that the arm was not included in the primary endpoint analysis. The reason and decision process beyond that statement are not reported in the registry record. These gaps do not establish that the analyses were inappropriate; they mark information needed for a fuller assessment of prespecification, missingness, and selective emphasis.

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: systemic lupus erythematosus (4.4%), pulmonary embolism (4.3%), pericarditis (2.2%), metrorrhagia (2.2%), ovarian cyst (2.2%).

The safety summaries report participants at risk and participants affected by serious and other adverse events in each group. In the 10 mg group, 4 of 45 participants were reported with serious adverse events and 20 of 45 with other adverse events. In the 50 mg group, the corresponding figures are 3 of 47 and 24 of 47. For 200 mg, they are 7 of 46 and 32 of 46; for placebo, 8 of 45 and 26 of 45.

These counts describe the registry’s event summaries and should be read separately from the primary efficacy analysis. The 200 mg group appears in the safety data even though it was omitted from the primary Week 24 efficacy analysis. Serious adverse-event terms listed in the record include systemic lupus erythematosus at 4.4%, pulmonary embolism at 4.3%, and pericarditis, metrorrhagia, ovarian cyst, and abdominal pain at 2.2% each. The record does not specify group attribution for these listed terms in the information summarized.

Deaths are not reported in the registry record’s safety summary. Event counts alone do not describe event severity, duration, causality assessment, or comparative risk with precision, and the record does not provide those details. These figures are descriptive and do not support a treatment recommendation.

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

The primary endpoint results describe how often participants met the registry’s complete SRI response definition at Week 24 in the analyzed dose groups. The 10 mg group’s reported response percentage was 59.9%, compared with 40.1% for placebo; the 50 mg group’s percentage was 39.2%. The sponsor’s model-based comparisons and unadjusted recalculations both leave uncertainty around the treatment contrasts, although they use different measures and methods.

The results do not establish that PF-04236921 works or does not work. A response proportion is a study outcome, not a recommendation for an individual. It does not show how every participant experienced the disease, which component of the composite determined response, or whether a difference would be meaningful in another setting. The trial’s 200 mg arm was excluded from the primary outcome analysis, so the primary results do not answer the same question for that dose.

The intervals and p-values should be interpreted as evidence from this analysis, not as direct probabilities that a treatment effect exists. The recalculated intervals include the no-difference value, while the sponsor’s reported intervals include the no-association value for an odds ratio. These estimates remain compatible with a range of effects. The registry record does not report enough information about missing outcome handling, the multiplicity strategy, or the full modeling details to resolve all interpretive uncertainty.

Safety summaries are also descriptive. They report affected participants and event terms, but do not by themselves establish causality or provide a complete account of event timing and severity. No individual medical decision can be made from these study-level data alone. The proper statistical reading is limited to what the registered outcomes, analysis methods, and reported results support.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through its endpoint definition, analysis population, and statistical method rather than through a single response percentage. The SRI is a composite that requires improvement across disease-activity measures while avoiding specified worsening and treatment-failure conditions. The percentage therefore summarizes a structured classification, not a simple change in one score.

The reported primary comparisons also demonstrate that the choice of effect measure matters. The sponsor reports odds ratios from mixed models, whereas the recalculations use risk differences from summary counts. These methods address related but distinct summaries of the data. The discrepancy flag makes it especially important to distinguish the sponsor’s inferential result from a simple unadjusted check, rather than presenting them as interchangeable.

The interrupted 200 mg arm is another important design and interpretation feature. It remains represented in safety reporting but is omitted from the primary efficacy analysis. Readers therefore need to track which groups contribute to which outcomes. A trial’s enrollment figure alone does not define the denominator for every analysis.

Finally, the record’s limited reporting on multiplicity, missing outcomes, and original sample-size assumptions constrains how confidently secondary results and precision can be assessed. These are not merely technical details: they determine what comparisons were planned, how incomplete observations were handled, and what range of effects the design was intended to detect. Transparent statistical interpretation identifies those boundaries rather than filling them with assumptions.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary analysis omits the 200 mg arm because dosing was prematurely terminated by sponsor decision. The registry does not report the reason for that decision beyond the statement itself, so the resulting omission cannot be further evaluated from this record. It means the primary efficacy results describe only the 10 mg and 50 mg comparisons with placebo, while safety summaries include 200 mg.

The endpoint population description says the Full Analysis Set includes randomized participants who received at least 1 dose, but also says the number analyzed for Week 24 was participants who completed through that visit. The record does not explain how the two descriptions relate in practice or how participants without Week 24 completion were handled. Missing-data methods, sensitivity analyses, and outcome-specific exclusion counts are not reported in the registry record.

The sponsor reports mixed-model odds ratios, but the model specification and adjustment details are not given in the information summarized. The recalculated comparisons are unadjusted and cannot reproduce the sponsor’s model. The discrepancy flag means the sponsor analysis should take precedence for the registry’s inferential result, while the simple calculations remain a separate descriptive check.

The statistical plan does not report a multiplicity strategy for the many outcomes and analyses. The original sample-size rationale, interim-analysis plan, and other prespecified analysis details are also not reported in the registry record. The secondary information includes baseline measurements, which do not by themselves establish treatment-related change. Finally, the safety record lists event counts and selected terms but does not report deaths, event timing, or full details of attribution in the summary available. These limitations restrict interpretation without proving that any particular result is biased.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Subcutaneous Treatment In Randomized Subjects To Evaluate Safety And Efficacy In Generalized Lupus Erythematosus — NCT01405196.
• Registry record last updated 2017-12-19; status last verified 2017-12.
• Results first posted 2017-12-19.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT01405196 is a completed randomized, double-blind, placebo-controlled, multicenter Phase 2 dose-ranging study of PF-04236921 in systemic lupus erythematosus. Enrollment was 183, with a recorded start of 2011-12 and primary completion in 2014-03. The primary outcome was SRI response at Week 24.

The reported primary outcome includes the 10 mg and 50 mg groups and placebo. Sponsor mixed-model odds ratios were 2.23 for 10 mg and 0.96 for 50 mg, each with a 90% confidence interval that includes one. Unadjusted risk-difference recalculations also have intervals spanning zero. Because the discrepancy flag is true, the sponsor analysis takes precedence. The 200 mg group was omitted from the primary endpoint analysis after premature termination of dosing but appears in safety reporting. The registry does not report key details on missing-data handling, multiplicity, or the original sample-size rationale.