A Study of Ustekinumab in Participants With Active Systemic Lupus Erythematosus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Ustekinumab in Participants With Active Systemic Lupus Erythematosus (NCT03517722), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving a Systemic Lupus Erythematosus Responder Index-4 (SRI-4) Composite Response at Week 52.

2. Clinical Question

The trial addressed a response question in participants with active SLE, a condition in which disease activity can involve multiple organ systems. The primary endpoint combined several requirements: improvement in the SLEDAI-2K score, no severe new BILAG domain activity and no more than one new moderate BILAG domain score, and no worsening in the Physician’s Global Assessment. This composite is intended to capture improvement while also limiting the possibility that deterioration in another assessment is overlooked.

The registry reports a Week 52 response of 43.9% in the ustekinumab group and 56.0% in the placebo group. These are the posted group percentages for the primary endpoint. They describe the observed results in this trial; by themselves, they do not establish why the groups differed or what would happen in other populations.

3. Trial Design

NCT03517722 is a Phase 3, randomized, double-blind, parallel-group study comparing ustekinumab with placebo in participants with active systemic lupus erythematosus. The registry lists an enrollment of 516. The study began on 2018-04-16, had a primary completion date of 2020-11-05, and is listed as terminated. The reason for termination is not reported in the registry record.

Participants were assigned to placebo or ustekinumab. The ustekinumab regimen listed for the double-blind period began with approximately 6 mg/kg intravenously at Week 0, followed by 90 mg subcutaneously at Week 8 and every 8 weeks thereafter through Week 48. The placebo description specifies matching intravenous and subcutaneous placebo on the corresponding schedule. The registry mentions an extension period and crossover for eligible participants, but the available descriptions do not give complete extension details.

Random allocation can help balance participant characteristics across groups on average, while double masking is intended to reduce the influence of treatment knowledge on participant experience, clinical assessment, and study conduct. These are general features of the design; the registry record does not report the allocation procedure’s implementation details or which parties were masked.

The primary endpoint was the percentage achieving an SRI-4 composite response at Week 52. The posted arm results include 116 participants for placebo and 173 for ustekinumab. These endpoint group sizes are not the same as the trial’s overall enrollment, and the registry record does not provide a complete account of how participants flowed from enrollment into this endpoint analysis. The stated start, completion, and termination information describes the registry record, but does not establish why the study ended when it did.

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: Participants received study drug up to Week 113, but were assessed for safety up to Week 130 (that is, after study termination).

Double Blind Period: Week 0-52

Reasons for not completing this period:

Open-label Extension Period: Week 52-113

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The projected full analysis set (FAS) was defined as those participants (participants who received at least 1 dose \[partial or complete,intravenous \[IV\] or subcutaneous \[SC\] of study agent) who should have had a given visit based upon their latest scheduled study visit. Participants were set to non-responders if they met treatment failure (TF) or had data missing.

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 a Systemic Lupus Erythematosus Responder Index-4 (SRI-4) Composite Response at Week 52, measured over Week 52.

The primary endpoint is the percentage of participants achieving an SRI-4 composite response at Week 52. The registry defines response as a reduction of at least 4 points in the SLEDAI-2K total score, no new BILAG A domain score, no more than one new BILAG B domain score, and no worsening in the Physician’s Global Assessment. The SLEDAI-2K assesses disease activity across organ systems; BILAG records domain-level activity; and the Physician’s Global Assessment is a clinician assessment of overall disease activity.

A composite endpoint brings several clinical assessments together under a prespecified response definition. In general, this can make the outcome more informative than a single measure when the condition has varied manifestations. It also means that a participant must satisfy the combined criteria, so the reported percentage depends on all components, not solely on a change in SLEDAI-2K.

The endpoint is reported as a percentage rather than as a continuous score, so it summarizes the share of participants meeting the response definition at the stated visit. The registry’s description of the projected full analysis set is cut off, and the complete endpoint-handling rules are not reported in the registry record. Interpretation should therefore distinguish the stated clinical definition from analysis details that are unavailable.

7. Results Posted in the Registry

• Ustekinumab: 43.9% (76/173) versus 56.0% (65/116) on control; risk difference -12.1 percentage points (95% CI -23.8 to -0.4), risk ratio 0.78 (0.62–0.99); unadjusted two-proportion z-test p = 0.044.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants With an SRI-4 Composite Response at Week 24

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Ustekinumab: 45.7% (79/173) versus 56.0% (65/116) on control; risk difference -10.4 percentage points (95% CI -22.1 to 1.3), risk ratio 0.81 (0.65–1.02); unadjusted two-proportion z-test p = 0.084.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ustekinumab and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With 50 Percent (%) Improvement in Joints With Pain and Signs of Inflammation (Active Joints) at Week 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:
  • Ustekinumab: 64.7% (99/153) versus 66.3% (67/101) on control; risk difference -1.6 percentage points (95% CI -13.6 to 10.3), risk ratio 0.98 (0.81–1.17); unadjusted two-proportion z-test p = 0.789.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ustekinumab and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Receiving Glucocorticoid at Baseline Who Achieved Change in Glucocorticoid Dose by Week 40 and Sustain That Change Through Week 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:
  • Ustekinumab: 44.3% (62/140) versus 29.3% (27/92) on control; risk difference 14.9 percentage points (95% CI 2.5 to 27.4), risk ratio 1.51 (1.04–2.18); unadjusted two-proportion z-test p = 0.022.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Ustekinumab than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover different aspects of SLE and treatment experience: an earlier SRI-4 response assessment, active-joint improvement, glucocorticoid-dose changes, cutaneous disease activity, and a combined glucocorticoid and SRI-4 outcome. The posted results do not form a uniformly one-directional pattern. This variety is important because each outcome measures a different construct, may use a different analysis population, and is assessed at its own time point.

These outcomes add context to the Week 52 primary endpoint, but they do not replace it. A response on a joint measure or a glucocorticoid-dose measure is not equivalent to meeting the SRI-4 composite. Likewise, an earlier SRI-4 assessment is not the same endpoint at the primary time point. The differences in outcome definitions mean that apparent agreement or disagreement across outcomes should be interpreted cautiously.

The registry lists multiple secondary outcomes and only one reported analysis. It does not report a multiplicity adjustment for the secondary comparisons. In general, evaluating many outcomes increases the chance that at least one comparison may appear noteworthy by chance, even when no corresponding underlying effect exists. Unadjusted secondary p-values therefore carry less evidential weight than a prespecified primary analysis interpreted within its stated statistical plan.

The registry record does not provide the full analysis hierarchy, whether particular secondary outcomes were designated confirmatory, or how multiplicity was handled. The secondary results are best treated as descriptive or supportive evidence unless further analysis-plan details are available. Their differing patterns should not be combined into a single claim about the overall effect.

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

• Time to First Flare
• Percentage of Participants With an SRI-4 Composite Response at Week 24
• Percentage of Participants With 50 Percent (%) Improvement in Joints With Pain and Signs of Inflammation (Active Joints) at Week 52
• Percentage of Participants Receiving Glucocorticoid at Baseline Who Achieved Change in Glucocorticoid Dose by Week 40 and Sustain That Change Through Week 52
• Percentage of Participants With at Least a 50% Improvement in the Cutaneous Lupus Erythematosus Disease Area and Severity Index (CLASI) Activity Score at Week 52
• Percentage of Participants Receiving Glucocorticoid at Baseline Who Achieved Change in Glucocorticoid Dose by Week 40, Sustained That Change Through Week 52, and Achieved an SRI-4 Composite Response at Week 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: each participant either meets the SRI-4 response definition at Week 52 or does not. The registry presents the outcome as a percentage of participants in each group. For this kind of outcome, a group percentage is readily interpretable as the observed fraction meeting the response criteria, but it does not describe the size or pattern of change among participants who did not meet the full composite definition.

What does the reported odds ratio represent?

The registry reports logistic regression and an odds ratio (OR). In general, logistic regression models the odds of a binary outcome, such as meeting the response definition, in relation to group assignment. An OR compares the modeled odds between groups. An OR below 1 indicates lower modeled odds in the group named in the comparison relative to the reference group, subject to the model’s coding and any adjustment terms. The registry reports an OR of 0.6 for ustekinumab relative to placebo, with a 95% confidence interval from 0.4 to 1.0 and p = 0.042.

Odds are not the same as probabilities or percentages. An OR should therefore not be read as a direct percentage-point difference in response. The observed group percentages provide the direct description of response frequency; the OR summarizes the reported regression comparison on the odds scale. The registry record does not report the regression covariates or other model specification details, so the extent and nature of adjustment cannot be determined from the record.

What does the unadjusted recalculation add?

The simple recalculation uses the posted group summaries to compare the response percentages without a regression model. Its risk-difference estimate is -0.121, and its unadjusted p-value is 0.044. In general, a risk difference expresses the difference between group probabilities on the probability scale, while the OR expresses a comparison on the odds scale. The recalculation is useful for understanding the raw contrast, but it is not a replacement for the sponsor’s reported regression analysis. The sponsor analysis takes precedence for describing the trial’s own reported inference.

Unadjusted comparisons do not account for covariates, and can differ from a regression result because of the model form, adjustment, or analysis details. The record does not give enough model information to determine which of these explains the small difference between the posted p-values. A p-value describes how compatible the observed data are with a specified null model under its assumptions; it is not an effect-size measure or a probability that the null hypothesis is true.

Why do confidence intervals matter?

A confidence interval expresses uncertainty around an estimated effect under the analysis assumptions. In general, narrower intervals indicate greater precision, while wider intervals indicate less precision. For an OR, the value 1 represents no difference in odds; for a risk difference, the value 0 represents no difference in probability. Whether an interval includes its no-difference value is one way to assess the range of estimates compatible with the data and method. The sponsor’s interval is rounded to 0.4 through 1.0, so its upper endpoint is displayed at the no-difference value.

Interval interpretation depends on the analysis population, outcome definition, and handling of unavailable outcomes. The registry provides endpoint group sizes and percentages, but a complete account of the estimation method and analysis population is not available. The meaning of the interval should therefore remain tied to the reported regression rather than extended to unreported assumptions.

Why can over-dispersion matter in other settings?

General statistical context: over-dispersion occurs when observed variability exceeds what a model assumes. It can make standard errors too small if the model does not accommodate that extra variability, leading to intervals that are too narrow and tests that appear more decisive than warranted. This is a general consideration for statistical modeling, not a reported issue in this trial. Over-dispersion is not specifically reported in the registry record, and it should not be presumed to have affected the logistic regression.

For a binary endpoint, the key considerations are how the response is defined, which participants are included, whether the model is adjusted, and how missing endpoint information is treated. The record identifies a projected full analysis set and provides a partial definition, but the remainder of that definition and the missing-data procedures are not reported in the registry record. These details affect how closely the posted estimate can be connected to the full randomized population.

11. Confidence Intervals and Precision

Precision concerns the uncertainty around an estimated group contrast, not whether the result is clinically important. The sponsor’s primary analysis reports an odds ratio of 0.6 with a 95% confidence interval from 0.4 to 1.0. The interval indicates that the reported estimate is not exact: values across a range remain compatible with the model and data. Because the displayed upper endpoint is 1.0, the interval reaches the value corresponding to no difference in odds at the precision shown in the registry.

The posted response percentages are 56.0% for placebo and 43.9% for ustekinumab. Each percentage is based on a finite endpoint group, and sampling variability means the observed percentages may not equal the underlying response probabilities. Confidence intervals help represent that uncertainty. The registry does not provide a confidence interval around each arm percentage in the posted primary outcome details, so those interval estimates are not reported in the registry record.

The unadjusted risk-difference recalculation also has uncertainty, but its detailed interval limits are not needed to read the sponsor’s reported result and are not reproduced. In general, a confidence interval for a risk difference is interpreted relative to 0, while an OR interval is interpreted relative to 1. These are different effect scales and should not be conflated.

The endpoint group sizes differ between arms, and the registry’s projected full analysis set description is incomplete. Precision is influenced by the amount of outcome information available, as well as the event frequency and analysis method. The available record does not establish why endpoint group sizes differ from one another or from overall enrollment. The reported interval is therefore best read as the uncertainty statement for the sponsor’s specified regression analysis, not as a complete account of every source of uncertainty.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations express participants per arm for 80% power and participants per arm for 90% power. They are planning examples based on the observed effect, not a reconstruction of the original trial’s design. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The registry’s own original sample-size assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under the planning assumptions, if that effect and the assumptions hold. The 90% power column gives the corresponding planning number for a 90% chance. These are prospective planning quantities: they describe what a future design might require, not the probability that the completed trial detected an effect.

Rows describe planning for 100%, 75%, and 50% of the observed effect. A smaller target effect is harder to distinguish from random variation, so the planning illustration calls for more participants per arm as the assumed effect becomes smaller. The figures are not observed power, and they do not indicate how likely the posted result is to be true.

For these binary endpoints, the reported planning unit is participants per arm, not total events. The record notes a different convention for time-to-event planning, where counts would be total events, but the outcomes discussed in these illustrations are percentages of participants with an event. These assumptions are generic planning inputs stated with the illustration; they should not be attributed to the trial’s original protocol or sample-size justification.

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 = 0.560; treatment proportion p₁ = 0.439; average p̄ = 0.500.
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 × 0.7019 = 0.5907.
4. n = (1.3859 + 0.5907)² / (-0.1210)² = 266.7, rounded up to 267 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 <- 0.560344827586207                          # control proportion
p1 <- 0.439306358381503                          # 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(3517722)
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 = 267 (80% power), 357 (90% power)
 75% of observed effect: n per arm = 475 (80% power), 635 (90% power)
 50% of observed effect: n per arm = 1,067 (80% power), 1,428 (90% power)
power.prop.test: 266.7 
Simulated power at n = 267 per arm: 0.808 (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 analysis uses logistic regression and gives an odds ratio of 0.6, a 95% confidence interval from 0.4 to 1.0, and p = 0.042. The simple unadjusted recalculation from the posted group summaries gives a risk difference of -0.121 and p = 0.044. The recalculation is a direct comparison of the observed percentages; the sponsor’s result is on the odds scale and comes from the reported regression method.

The two p-values are close but not identical. That is not inherently contradictory: analyses on different scales or with different modeling details can yield somewhat different estimates and tests. The registry does not report the regression covariates or complete model specification, so the source of the difference cannot be determined from the record. The discrepancy flag is false, and the sponsor’s own analysis takes precedence when describing the study’s reported analysis.

The sponsor’s confidence interval is rounded and reaches 1.0 at its upper limit. It should be interpreted together with the OR, the observed group percentages, and the stated endpoint. The recalculation is a supplementary unadjusted description, not a substitute for the registry-reported model or evidence that the model’s unreported details can be reconstructed.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates multiple outcomes, time points, or comparisons. In general, each additional statistical test creates another opportunity for a chance finding. A prespecified strategy can control the overall error rate, for example by defining a testing order or adjusting significance thresholds. The registry lists multiple secondary outcomes, but a multiplicity strategy is not reported in the registry record. The record lists one reported analysis; that does not establish the full statistical testing plan or whether other analyses were conducted.

The primary outcome has a stated time point and response definition, and the registry gives a sponsor-reported logistic-regression analysis. However, the complete statistical analysis plan, model covariates, and any interim analyses are not reported in the registry record. No interim analysis should be assumed. Without those details, the reported primary analysis can be described, but its full prespecification and relationship to any testing hierarchy cannot be verified from the record.

Missing outcome data can influence a binary response analysis, particularly if participants without an observed outcome are handled differently from participants with observed outcomes. The primary endpoint description refers to a projected full analysis set and begins to define it using participants who received at least one dose and who should have had a given visit, but the description is incomplete. The full missing-data rules, including how unavailable Week 52 outcomes were classified or imputed, are not reported in the registry record.

The registry’s endpoint group sizes are not the same as overall enrollment. The record does not provide a complete participant flow or explain the reasons for exclusions from each endpoint analysis. It also does not report enough detail to determine how the analysis population relates to all randomized participants. These gaps limit assessment of the potential influence of missing data and deviations from the intended analysis population.

These omissions do not establish that the analysis was inappropriate; they mark what cannot be evaluated from the registry entry. Interpretation should distinguish the reported estimates from unreported design and analysis decisions, rather than filling those gaps with assumptions.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: systemic lupus erythematosus (1.9%), covid-19 (1.3%), pneumonia (1.3%), acute myocardial infarction (1.1%), bradycardia (1.1%).

The registry reports serious adverse events and other adverse events for groups described across different treatment periods. Before entering the long-term extension, the placebo group had 208 participants at risk, 28 with serious adverse events, 60 with other adverse events, and 1 death. After entering the extension, the placebo-to-ustekinumab group had 88 participants at risk, 5 with serious adverse events, 3 with other adverse events, and 0 deaths. The ustekinumab group through Week 113 had 307 participants at risk, 44 with serious adverse events, 79 with other adverse events, and 5 deaths.

These groups represent different treatment periods and descriptions, so their counts should not be treated as a direct randomized comparison over a common follow-up period. The registry also lists serious-event terms including systemic lupus erythematosus at 1.9%, Covid-19 at 1.3%, pneumonia at 1.3%, acute myocardial infarction at 1.1%, bradycardia at 1.1%, and visual impairment at 1.1%.

Event counts alone do not establish that a treatment caused an event, and the registry figures do not provide full exposure-adjusted rates or a complete safety analysis. The reason for termination is not reported in the registry record, and no causal interpretation of the safety counts should be inferred from termination status.

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

The primary result describes the proportion of participants meeting a specific composite response definition at Week 52. The posted percentages are 43.9% for ustekinumab and 56.0% for placebo. The sponsor’s logistic-regression analysis reports an OR of 0.6 with a 95% confidence interval from 0.4 to 1.0 and p = 0.042. Together, these figures describe the observed endpoint and the sponsor’s modeled comparison for this trial.

They do not establish the biological reason for the difference, the effect in every participant, or the result that would occur in another setting. A composite response combines SLEDAI-2K, BILAG, and Physician’s Global Assessment criteria. A participant may fail to meet the endpoint for different reasons, and the overall response percentage does not show which component most often determined response or nonresponse.

The result also does not establish an effect on every manifestation of SLE. The secondary outcomes measure distinct domains and have different time points and populations. Their results cannot be substituted for the primary endpoint or treated as a single unified measure of disease activity.

The registry lists the study as terminated, but the reason is not reported in the registry record. Termination status alone does not explain the primary findings, indicate that a particular result caused the decision, or provide evidence about the treatment’s effects. The full analysis plan, complete missing-data handling, and full description of the analysis population are also unavailable in the registry record, limiting how completely the reported estimates can be assessed.

Statistical evidence should be read alongside the endpoint definition, precision, study design, and completeness of reporting. The estimates describe this trial’s posted data; they are not medical advice and do not by themselves establish whether a treatment should be used.

18. Why This Trial Matters Statistically

This trial illustrates why an outcome definition matters as much as the headline percentage. The SRI-4 endpoint requires improvement on one disease activity measure while also imposing limits on new BILAG activity and worsening in the Physician’s Global Assessment. The reported percentage therefore represents a multidimensional response rule rather than a single symptom, laboratory result, or score.

It also shows why the analysis scale needs to be identified. The group percentages communicate the observed response frequency, whereas the sponsor’s logistic regression reports an odds ratio. The unadjusted recalculation uses a risk difference and produces a slightly different p-value. These measures answer related but not identical statistical questions. Keeping the scales and methods distinct avoids treating them as interchangeable.

The secondary endpoints make another important point: different outcomes can show different patterns without being logically inconsistent. Joint improvement, glucocorticoid-dose change, and a composite SRI-4 response represent different clinical dimensions and use different endpoint populations. Their results require attention to multiplicity and to the status of each outcome in the analysis plan.

Finally, the registry record demonstrates how incomplete reporting can constrain interpretation. It gives the trial design, primary endpoint, selected results, and safety counts, but does not report the complete statistical analysis plan, the reason for termination, or full missing-data rules. A careful reading can describe the posted evidence while keeping those limitations visible, rather than turning incomplete information into 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 registry record does not report why the study was terminated. It also does not provide the complete statistical analysis plan, including model covariates, interim analyses, or a multiplicity strategy. These omissions limit assessment of how the reported primary analysis fits into the full planned testing framework.

The primary endpoint population description is incomplete: it identifies a projected full analysis set and begins to state eligibility based on treatment receipt and scheduled visits, but the remaining definition is not available. The record does not provide complete participant flow, reasons for endpoint exclusions, or the rules used for missing Week 52 outcomes. These details matter for understanding how the posted endpoint percentages relate to the randomized groups.

The overall enrollment is 516, while the primary endpoint group sizes are 116 for placebo and 173 for ustekinumab. The record does not explain the relationship between those figures or give enough information to reconstruct all analysis denominators. Endpoint groups also differ across secondary outcomes, so comparisons across outcomes should not be assumed to use the same participant set.

The sponsor’s reported regression is identified as logistic regression, but its full specification is not reported. The unadjusted recalculation is therefore a useful raw comparison, not a means of reproducing the sponsor’s model. Safety counts also come from groups described across different treatment periods, and the registry does not provide a common exposure-adjusted comparison in the available details.

These limitations describe gaps in the registry record; they do not show that a particular analysis decision was wrong. They define the boundaries for interpreting the posted estimates.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Ustekinumab in Participants With Active Systemic Lupus Erythematosus — NCT03517722.
• Registry record last updated 2025-04-29; status last verified 2025-04.
• Results first posted 2022-03-09.
• 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

NCT03517722 is a randomized, double-blind, parallel-group Phase 3 study of ustekinumab versus placebo in participants with active systemic lupus erythematosus who had not adequately responded to one or more standard of care treatments. The registry lists enrollment of 516, a start date of 2018-04-16, primary completion on 2020-11-05, and status as terminated.

The primary endpoint was SRI-4 response at Week 52. The posted response percentages were 56.0% for placebo and 43.9% for ustekinumab. The sponsor-reported logistic-regression result was an OR of 0.6, a 95% confidence interval from 0.4 to 1.0, and p = 0.042. The registry also includes secondary outcomes and safety counts, but full analysis details, missing-data rules, and the reason for termination are not reported in the registry record.