A Study to Compare Upadacitinib (ABT-494) to Placebo in Adults With Rheumatoid Arthritis on Stable Dose of Conventional Synthetic Disease-Modifying Antirheumatic Drugs (csDMARDs) With an Inadequate Response or Intolerance to Biologic DMARDs: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Compare Upadacitinib (ABT-494) to Placebo in Adults With Rheumatoid Arthritis on Stable Dose of Conventional Synthetic Disease-Modifying Antirheumatic Drugs (csDMARDs) With an Inadequate Response or Intolerance to Biologic DMARDs (NCT02706847), a randomized phase 3 study. The primary outcome is Percentage of Participants With an American College of Rheumatology 20% (ACR20) Response at Week 12.

2. Clinical Question

The central statistical question is about the difference in the proportion meeting a prespecified response definition, not about an average change in a single symptom or laboratory measurement. The registry reports results for the placebo group and both upadacitinib dose groups, together with confidence intervals and sponsor-reported comparisons. The reported comparisons concern the response-rate difference between each dose group and placebo.

The findings apply to the trial population and the endpoint definition used in the record. They do not by themselves establish how results would generalize to people outside the stated population, to other treatment settings, or to outcomes not measured by the registry endpoints. The record describes a randomized, double-blind study, but does not report every detail needed to assess implementation of randomization or blinding.

3. Trial Design

The registry describes a Phase 3, randomized, quadruple-masked, parallel-group study sponsored by AbbVie. It lists enrollment of 499 and the condition as rheumatoid arthritis. The study is marked completed. The listed study dates are 2016-03-15 for start and 2017-04-03 for primary completion.

The first study period extended from Day 1 to Week 24. Its stated objective was to compare the safety and efficacy of upadacitinib 15 mg once daily and 30 mg once daily with placebo for signs and symptoms in participants receiving stable csDMARDs who had an inadequate response or intolerance to at least 1 biologic DMARD. For the primary Week 12 comparison, the groups were placebo, upadacitinib 15 mg, and upadacitinib 30 mg. The registry lists 169 participants in the placebo group, 164 in the 15 mg group, and 165 in the 30 mg group for that outcome.

The arm descriptions indicate that placebo was used during the first 12 weeks, followed by upadacitinib for the remainder of Period 1 in the placebo-assigned groups. Participants assigned upadacitinib from the start continued their assigned dose during Period 1. The second period ran from Week 24 to Week 260 and was described as evaluating longer-term safety, tolerability, and efficacy among participants completing Period 1. The 30 mg groups could switch to 15 mg after implementation of Protocol Amendment 4.

These design details distinguish the short placebo-controlled comparison from later follow-up under upadacitinib treatment. The Week 12 primary results address the former comparison; later-period safety summaries have different exposure periods and should not be treated as a continuation of the same placebo comparison.

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 were randomized in a 1:1:2:2 ratio to one of the four treatment groups below. Randomization was stratified by the number of previous bDMARDs used and geographic region.

Period 1: Day 1 to Week 12

Reasons for not completing this period:

Period 1: Week 12 to Week 24

Reasons for not completing this period:

Period 2: Week 24 to Week 260

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set; participants who prematurely discontinued from study drug prior to Week 12 or for whom ACR data were missing at Week 12 were considered non-responders.

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: The full analysis set (FAS) included all randomized participants who received at least 1 dose of study drug. The 2 placebo groups were combined for analysis of data through Week 12.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With an American College of Rheumatology 20% (ACR20) Response at Week 12, measured over Baseline and Week 12.

The primary endpoint is the percentage of participants with an American College of Rheumatology 20% response at Week 12, measured from baseline. ACR20 is a composite response definition: participants had to meet the specified improvement threshold in both the 68-tender joint count and the 66-swollen joint count, as well as in at least 3 of 5 additional measures. Those measures were physician global assessment of disease activity, patient global assessment of disease activity, patient assessment of pain, the Health Assessment Questionnaire Disability Index, and high-sensitivity C-reactive protein.

Using a composite endpoint captures change across multiple aspects of rheumatoid arthritis rather than relying on a single measure. Requiring improvement in joint counts and several additional measures makes the definition broader than improvement in only one symptom or assessment. ACR20 is expressed as a response proportion: each participant either met the definition or did not under the endpoint rules.

The registry identifies ACR20 at Week 12 as the primary endpoint for United States/FDA regulatory purposes. The primary population was the full analysis set. Participants who prematurely discontinued study drug before Week 12, or whose ACR data were missing at Week 12, were classified as non-responders. That rule is important to interpretation because the reported proportions reflect both the response criteria and the registry’s treatment of missing endpoint data.

As with any composite response measure, the endpoint summarizes a defined set of clinical assessments and does not describe every aspect of disease status, long-term outcomes, or individual participant experience. The posted result is a group-level response proportion rather than a prediction for any particular person.

7. Results Posted in the Registry

• Upadacitinib 15 mg: 64.6% (106/164) versus 28.4% (48/169) on control; risk difference 36.2 percentage points (95% CI 26.2 to 46.2), risk ratio 2.28 (1.75–2.97); unadjusted two-proportion z-test p = <0.001.
• Upadacitinib 30 mg: 56.4% (93/165) versus 28.4% (48/169) on control; risk difference 28.0 percentage points (95% CI 17.8 to 38.1), risk ratio 1.98 (1.51–2.61); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

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

Percentage of Participants With an American College of Rheumatology 50% (ACR50) Response at Week 12

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Upadacitinib 15 mg: 34.1% (56/164) versus 11.8% (20/169) on control; risk difference 22.3 percentage points (95% CI 13.6 to 31.1), risk ratio 2.89 (1.82–4.59); unadjusted two-proportion z-test p = <0.001.
  • Upadacitinib 30 mg: 35.8% (59/165) versus 11.8% (20/169) on control; risk difference 23.9 percentage points (95% CI 15.1 to 32.7), risk ratio 3.02 (1.91–4.78); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Upadacitinib 15 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Upadacitinib 30 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With an American College of Rheumatology 70% (ACR70) Response at Week 12

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Upadacitinib 15 mg: 11.6% (19/164) versus 6.5% (11/169) on control; risk difference 5.1 percentage points (95% CI -1.1 to 11.2), risk ratio 1.78 (0.87–3.62); unadjusted two-proportion z-test p = 0.106.
  • Upadacitinib 30 mg: 23.0% (38/165) versus 6.5% (11/169) on control; risk difference 16.5 percentage points (95% CI 9.1 to 23.9), risk ratio 3.54 (1.87–6.68); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Upadacitinib 15 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 proportion with the event is statistically higher for Upadacitinib 30 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With an American College of Rheumatology 20% (ACR20) Response at Week 1

• 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:
  • Upadacitinib 15 mg: 27.4% (45/164) versus 10.7% (18/169) on control; risk difference 16.8 percentage points (95% CI 8.5 to 25.1), risk ratio 2.58 (1.56–4.26); unadjusted two-proportion z-test p = <0.001.
  • Upadacitinib 30 mg: 24.8% (41/165) versus 10.7% (18/169) on control; risk difference 14.2 percentage points (95% CI 6.1 to 22.3), risk ratio 2.33 (1.40–3.89); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Upadacitinib 15 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Upadacitinib 30 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover other response thresholds and measures of disease activity, function, and health status. Across the binary response outcomes with posted results, the overall direction generally favors the upadacitinib groups over placebo at the reported assessment times. The pattern is broadly consistent with the primary ACR20 finding, while the size and precision of contrasts vary by endpoint and dose. Not every comparison has the same strength of statistical evidence, so the secondary results should not be treated as interchangeable with the primary result.

The secondary outcomes add context because they examine response criteria of different stringency and include measures beyond the primary composite. They can help readers see whether the primary pattern is accompanied by findings across related clinical assessments. However, consistency in direction does not establish that every outcome has been confirmed independently, and secondary measures do not alter the definition or analysis population of the primary endpoint.

Unadjusted secondary results carry less weight for confirmatory claims when multiple outcomes and comparisons are examined. In general, testing many hypotheses increases the opportunity for chance findings unless the statistical plan controls the overall error rate or specifies a hierarchy. The registry record does not report whether secondary tests were adjusted for multiplicity, whether a testing sequence was prespecified, or how the family of outcomes was defined. Their p-values and confidence intervals therefore need to be read with that uncertainty about the analysis plan in mind.

The record lists additional outcomes, including changes in disease activity, disability, and physical health status, but complete posted numeric results for all listed secondary measures are not included in the registry record described for this analysis. Their results should not be inferred from the binary response findings. The secondary evidence is best understood as supportive context, with the prespecified primary endpoint retaining the clearest role in the registry’s stated regulatory question.

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

• Change From Baseline in in Disease Activity Score 28 (CRP) at Week 12
• Change From Baseline in Health Assessment Questionnaire Disability Index (HAQ-DI) at Week 12
• Change From Baseline in Short-Form 36 (SF-36) Physical Component Score (PCS) at Week 12
• Percentage of Participants With an American College of Rheumatology 50% (ACR50) Response at Week 12
• Percentage of Participants With an American College of Rheumatology 70% (ACR70) Response at Week 12
• Percentage of Participants With an American College of Rheumatology 20% (ACR20) Response at Week 1

9. Statistical Interpretation

10. Statistical Methods Explained

For this binary endpoint, each participant is classified as an ACR20 responder or a non-responder at Week 12. The response percentage is the proportion classified as a responder within each group. A risk difference, also called a response-rate difference here, compares the group proportions by subtracting the comparator proportion from the intervention proportion. Positive differences in these reported comparisons indicate a higher observed response percentage in the upadacitinib group than in placebo. The posted estimates express those differences in percentage points.

What does randomization contribute?

In general, random assignment is intended to make treatment groups comparable, on average, with respect to measured and unmeasured baseline characteristics. That supports interpreting between-group differences as treatment comparisons rather than simple contrasts between self-selected groups. Randomization does not guarantee that every baseline characteristic is identical across groups, and the registry record does not report enough detail to assess the randomization procedure or allocation concealment.

The study is described as randomized, parallel-group, and quadruple-masked. In general, masking can reduce the risk that expectations influence participant reporting, clinical assessments, or study conduct. The registry record does not identify all parties covered by the masking label or describe how masking was maintained. The stated design supports understanding the intended comparison, but the label alone is not a complete account of implementation.

How should a confidence interval be understood?

In general, a confidence interval describes the range of estimates compatible with the data and the method used, at the stated confidence level. A narrower interval indicates greater precision for the estimated contrast, while a wider interval indicates more uncertainty. It does not show the probability that a fixed true effect lies inside that particular calculated interval. The sponsor reports 95% confidence intervals for the primary response-rate differences.

The registry’s sponsor analyses use the Cochran-Mantel-Haenszel method and report response-rate differences. In general, this method can estimate a treatment contrast while accounting for stratification factors. The registry record does not state which strata were used in these analyses, so that aspect of the sponsor model cannot be evaluated from the record alone. The unadjusted recalculations based on posted summary statistics are not substitutes for the sponsor’s analysis.

What does a p-value add?

In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions held. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. The sponsor reports p < 0.001 for both primary comparisons. The effect estimate and confidence interval remain important because they describe the direction, scale, and uncertainty of the observed contrast.

The reported endpoint is a percentage, but it is still a binary outcome at the participant level: responder or non-responder. General statistical methods for binary data therefore focus on event proportions and contrasts between proportions. The interpretation of those contrasts depends on the endpoint definition, the analysis population, and the way missing values are handled. Here, the stated rule classifies participants with missing Week 12 ACR data or early study-drug discontinuation as non-responders.

Why do analysis populations and missing-data rules matter?

In general, an analysis population determines which participants contribute to an estimate, while a missing-data rule determines how unavailable outcomes are represented or modeled. Treating missing outcomes as non-response is one explicit approach; it makes the result reflect the assumption that those participants did not meet the endpoint. Other approaches can yield different estimates when the missingness pattern or assumptions differ. The registry record does not report sensitivity analyses or a fuller account of missing-data handling beyond the stated non-responder rule.

Multiple outcomes and comparisons also raise a general multiplicity issue. If many hypotheses are tested, the chance of at least one apparently significant result can increase unless the analysis plan addresses that issue. The registry record lists multiple primary and secondary analyses, but does not report whether multiplicity adjustments or a testing hierarchy were used. Thus, unadjusted secondary p-values should be read as exploratory or supportive evidence rather than treated as definitive confirmatory findings.

11. Confidence Intervals and Precision

The primary sponsor-reported response-rate difference for upadacitinib 15 mg versus placebo is 36.2, with a 95% confidence interval from 26.2 to 46.2. For upadacitinib 30 mg versus placebo, the difference is 28.0, with a 95% confidence interval from 17.8 to 38.1. These intervals are expressed in percentage points and summarize uncertainty in the estimated group contrasts. Both reported intervals are on the positive side of no difference.

A confidence interval is useful because the point estimate alone does not show how much uncertainty accompanies an estimate. In general, an interval that spans a broad range permits a wider range of plausible effect sizes than a narrower interval. Neither interval describes the range of outcomes expected for individual participants, and neither guarantees that the underlying effect is contained within the endpoints of the calculated interval.

The interval estimates are conditional on the analysis method, endpoint definition, and population used. The registry reports that the sponsor used the Cochran-Mantel-Haenszel method, but does not report the stratification details in the record. The full analysis set and non-responder treatment of specified missing outcomes also form part of the interpretation. Alternative analysis choices could produce different estimates or uncertainty intervals; sensitivity results are not reported in the registry record.

The two dose comparisons are each against placebo. Their intervals should not be used as a formal test comparing the doses with one another. The registry does not report a direct dose-to-dose comparison for the primary endpoint. Confidence intervals also do not convey every source of uncertainty, such as uncertainty about generalizing from this trial population to people outside the stated eligibility 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 sample-size figures are planning illustrations based on the observed effect, not the original design calculation. For this binary outcome, the displayed figures are participants per arm, not total event counts. The planning assumptions listed in the registry are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for each illustration is the stated fraction of the observed effect. The registry record does not report the trial’s original sample-size justification or its original design assumptions.

The 80% power column gives the illustrated number of participants per arm under which a study would have an 80% chance of detecting the specified effect, assuming the planning model and other stated assumptions. The 90% power column describes the corresponding planning target for a 90% chance of detection. These are design-planning concepts, not descriptions of what happened in this completed trial. This is not observed power.

The rows that use 100% of the observed effect illustrate planning around an effect as large as the one estimated in the posted results. Rows using 75% or 50% of the observed effect illustrate smaller target effects. Smaller effects are generally harder to distinguish from random variation, so they require more participants per arm to achieve the same target power under otherwise unchanged assumptions. This relationship is reflected in the increasing sample-size requirements as the assumed effect becomes smaller.

The calculations are illustrations rather than recommendations for a future study. They use an observed effect, which is itself uncertain, and do not establish the assumptions that informed this trial’s design. The trial’s own sample-size rationale is not reported in the registry record. Interpret the curves and entries as conditional planning aids rather than evidence about the trial’s power after its results were observed.

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 = 0.284; treatment proportion p₁ = 0.646; average p̄ = 0.465.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7054 = 1.3825.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6572 = 0.5531.
4. n = (1.3825 + 0.5531)² / (0.3623)² = 28.5, rounded up to 29 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 <- 0.284023668639053                          # control proportion
p1 <- 0.646341463414634                          # 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(2706847)
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 = 29 (80% power), 38 (90% power)
 75% of observed effect: n per arm = 51 (80% power), 68 (90% power)
 50% of observed effect: n per arm = 111 (80% power), 148 (90% power)
power.prop.test: 28.5 
Simulated power at n = 29 per arm: 0.804 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary analyses compare each upadacitinib dose with placebo using the Cochran-Mantel-Haenszel method. For 15 mg versus placebo, the reported response-rate difference is 36.2, the 95% confidence interval is 26.2 to 46.2, and p < 0.001. For 30 mg versus placebo, the reported difference is 28.0, the 95% confidence interval is 17.8 to 38.1, and p < 0.001. Both analyses are labeled superiority in the registry.

The recalculated comparisons are simple, unadjusted calculations from the posted summary statistics. They are useful as a check on the direction and approximate scale of the contrasts, but they do not reproduce the sponsor’s analysis method. The discrepancy flag is false, so the record does not indicate a discrepancy requiring a different interpretation. Where a sponsor analysis is reported, it remains the primary analysis to cite rather than treating an unadjusted recalculation as a replacement.

The registry does not report which stratification factors, if any, were included in the Cochran-Mantel-Haenszel analyses. Consequently, the relationship between the sponsor estimates and a particular adjustment structure cannot be assessed from the registry record alone. The recalculation also does not supply missing detail about the sponsor’s analysis plan, multiplicity handling, or sensitivity analyses.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple outcome measures and analyses, including the primary ACR20 endpoint and several secondary assessments. Whenever multiple hypotheses are tested, there is a general risk that some results may appear statistically persuasive by chance alone. Common approaches to address this include adjustment of significance thresholds, a hierarchical testing plan, or explicit designation of exploratory analyses. The registry record does not report whether any such approach was used for the primary and secondary outcomes.

The sponsor’s primary analyses are reported as superiority comparisons, with p-values and 95% confidence intervals. The registry record does not specify whether the primary comparisons were adjusted for multiplicity, whether the dose comparisons followed a formal testing sequence, or how testing across secondary outcomes was handled. That missing information limits interpretation of the collection of p-values, especially for secondary endpoints. It does not change the numerical estimates reported for the primary comparisons, but it matters when making claims across the full set of outcomes.

The primary analysis population is identified as the full analysis set. The record states that participants who discontinued study drug before Week 12 or had missing ACR data at Week 12 were considered non-responders. This rule is clear for the primary response endpoint, but the registry record does not report additional sensitivity analyses that test other missing-data assumptions. It also does not provide enough detail to assess the timing or extent of missing outcome data beyond the rule itself.

In general, missingness can affect an estimate if the probability of missing data is related to outcome status or treatment experience. A non-responder rule avoids excluding those participants from the response proportion, but it does not remove the need to understand why data were missing or how alternative assumptions might affect results. Those details are not reported in the registry record.

The record also does not report an interim-analysis plan, stopping rules, or the full statistical analysis plan. Their absence should not be taken as evidence that a procedure was or was not used; it means the registry record does not document it. These gaps call for caution when interpreting results across numerous endpoints and analyses, particularly when moving beyond the sponsor-reported primary comparisons.

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: pneumonia (3.8%), pulmonary embolism (3.0%), osteoarthritis (2.9%), deep vein thrombosis (2.1%), acute myocardial infarction (1.7%).

The registry reports serious adverse events and deaths across the placebo-controlled first 12 weeks and longer treatment periods. During Weeks 1-12, serious adverse events were reported for 0 participants in the placebo group, 9 in the upadacitinib 15 mg group, and 12 in the upadacitinib 30 mg group. Deaths reported for those groups during the same period were 0, 0, and 1, respectively. These are counts, and the registry lists the corresponding groups at risk as 169, 164, and 165.

For the longer summaries, the registry reports 87 serious adverse events and 9 deaths in the upadacitinib 15 mg Weeks 1-260 group, and 71 serious adverse events and 5 deaths in the upadacitinib 30 mg Weeks 1-260/switch group. The separate upadacitinib 15 mg after-switch group reports 21 serious adverse events and 2 deaths. The groups at risk are listed as 236, 240, and 138, respectively.

The record also identifies pneumonia, pulmonary embolism, osteoarthritis, deep vein thrombosis, acute myocardial infarction, and COVID-19 among the leading serious adverse event terms, with the listed percentages ranging from 1.7% to 3.8%. The long-period group descriptions involve different exposure histories, and the after-switch summary should not be interpreted as a randomized comparison with placebo. Counts alone do not establish causation or permit a complete comparative safety assessment; the registry record does not provide the full clinical context for each event.

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

The posted primary result shows that the Week 12 ACR20 response percentage was higher in each upadacitinib group than in the placebo group under the endpoint and missing-data rules recorded in the trial registry. The sponsor-reported response-rate differences are positive, and both corresponding confidence intervals lie above no difference. The findings are evidence about this defined comparison in the enrolled trial population, not a guarantee of an outcome for an individual participant.

The result does not establish that upadacitinib improves every symptom, function measure, or longer-term outcome. ACR20 is a composite response threshold based on joint counts and additional measures. A participant-level response is not the same as complete disease control, and the group percentages do not indicate how much any one person changed. The trial’s primary endpoint also does not answer questions about outcomes that were not assessed or reported.

The result does not establish a difference between the 15 mg and 30 mg doses. The posted primary sponsor comparisons are each against placebo, and the registry does not report a direct statistical comparison between doses. The observed response percentages differ numerically, but that ordering alone is not a formal dose-to-dose test.

The Week 12 placebo-controlled result should also be separated from the later period. After Week 12, placebo participants began upadacitinib, and the second period evaluated longer-term upadacitinib treatment. The later safety summaries therefore have different treatment histories and do not preserve a placebo comparison through Week 260.

Finally, statistical evidence does not by itself determine the clinical importance of a difference. Confidence intervals help describe precision in the estimated contrast, while the registry’s endpoint definition and population set the scope of inference. Missing details about multiplicity, the complete statistical plan, and sensitivity to missing-data assumptions remain relevant when judging how broadly to interpret the findings.

18. Why This Trial Matters Statistically

This trial is statistically informative because it reports a randomized, masked, placebo-controlled comparison for a clearly defined binary response endpoint in a population with rheumatoid arthritis and prior inadequate response or intolerance to biologic DMARDs. The ACR20 endpoint combines joint-count improvement with additional assessments, and the registry specifies how missing Week 12 data and early treatment discontinuation were classified. Those features make the target comparison and the response rule relatively clear.

Reporting both group response percentages and between-group differences supports interpretation beyond a significance test alone. The confidence intervals communicate the precision of the estimated contrasts, while the sponsor’s Cochran-Mantel-Haenszel analyses provide the registry’s primary inferential results. The availability of results for two dose groups also shows why direct comparisons should not be inferred from separate comparisons against placebo.

The study also illustrates the importance of separating a controlled early comparison from longer follow-up. Placebo treatment ended after Week 12, and later treatment histories included upadacitinib and, for some participants, a dose switch. Consequently, Week 12 efficacy comparisons and later safety summaries answer different questions and should be interpreted on their own terms.

At the same time, a registry record is not a substitute for a complete statistical analysis plan or full report. The record does not specify multiplicity handling, all analysis details, or sensitivity analyses for missing data. These omissions matter for judging the strength of claims across a collection of outcomes, even when the primary estimates are clearly reported. The trial is a useful example of how effect estimates, uncertainty intervals, endpoint rules, and analysis-plan transparency all contribute to statistical interpretation.

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 gives important design and endpoint information, but some details needed for a full assessment are not reported in the registry record. These include the original sample-size justification, the complete statistical analysis plan, the randomization and allocation-concealment procedures, and the parties included in quadruple masking. The record also does not provide the stratification details for the Cochran-Mantel-Haenszel analyses.

Multiplicity handling is not reported. This is especially relevant because the record lists multiple outcomes and comparisons. Without a reported testing hierarchy or adjustment approach, secondary p-values should not be treated as definitive confirmation across the full outcome set. The record also does not report whether interim analyses were planned or conducted.

The primary missing-data rule is stated, but sensitivity analyses using alternative assumptions are not reported. The available information does not establish whether the non-responder classification is robust to other reasonable approaches or whether missingness differed in ways that could affect the estimates. The record also does not provide a complete account of missing data for every secondary outcome.

For safety, the reported summaries use different follow-up periods and treatment histories. The longer-period groups include participants who continued or switched treatment, and they are not equivalent to a continued placebo-controlled comparison. Event counts alone do not describe timing, severity, relatedness, exposure-adjusted rates, or the full context of individual events; those details are not reported in the registry record used for this analysis.

Finally, the primary endpoint addresses response at Week 12 in the stated trial population. It does not on its own establish longer-term comparative efficacy, effects on unreported outcomes, or generalizability beyond the enrolled population. These limitations define the scope of the posted results rather than negate the reported comparisons.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Compare Upadacitinib (ABT-494) to Placebo in Adults With Rheumatoid Arthritis on Stable Dose of Conventional Synthetic Disease-Modifying Antirheumatic Drugs (csDMARDs) With an Inadequate Response or Intolerance to Biologic DMARDs — NCT02706847.
• Registry record last updated 2023-02-08; status last verified 2023-01.
• Results first posted 2019-10-07.
• 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

NCT02706847 is a completed Phase 3 randomized, quadruple-masked, parallel-group study sponsored by AbbVie. It enrolled adults with moderately to severely active rheumatoid arthritis receiving stable csDMARDs who had an inadequate response or intolerance to biologic DMARDs. The primary endpoint was ACR20 response at Week 12, with missing Week 12 ACR data and premature study-drug discontinuation classified as non-response.

The registry reports higher Week 12 ACR20 percentages in both upadacitinib dose groups than in placebo. The sponsor’s reported response-rate differences versus placebo were 36.2 for 15 mg and 28.0 for 30 mg, with p < 0.001 for each comparison. The findings apply to the endpoint, population, and first-period comparison described in the record.

The registry also describes a later treatment period through Week 260, including dose switching in the 30 mg group. Later safety summaries reflect those differing treatment histories and are not a placebo-controlled comparison. Details about multiplicity handling, the original sample-size rationale, and several elements of the full statistical plan are not reported in the registry record.