A Study of the Effectiveness and Safety of Ustekinumab (STELARA) and CNTO 1959 Administered Under the Skin of Patients With Active Rheumatoid Arthritis, Despite Existing Methotrexate Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of the Effectiveness and Safety of Ustekinumab (STELARA) and CNTO 1959 Administered Under the Skin of Patients With Active Rheumatoid Arthritis, Despite Existing Methotrexate Therapy (NCT01645280), a randomized phase 2 study. The primary outcome is Percentage of Participants With American College of Rheumatology 20 (ACR 20) Response at Week 28.

2. Clinical Question

The study addressed signs and symptoms of rheumatoid arthritis among participants whose disease remained active while they were receiving methotrexate. The primary endpoint used a response threshold rather than a continuous score: participants had to meet the specified improvement criteria across joint counts and other core measures. The registry record lists four comparisons with placebo, one for each active-treatment group.

The posted results show ACR 20 response percentages of 40.0 for placebo, 52.7 for ustekinumab 90 mg every 8 weeks, 54.5 for ustekinumab 90 mg every 12 weeks, 44.4 for CNTO 1959 200 mg every 8 weeks, and 38.2 for CNTO 1959 50 mg every 8 weeks. These are descriptive percentages in the recorded groups, not by themselves proof of a difference between groups. The uncertainty intervals and reported analyses matter when judging how precisely the comparisons are estimated.

The registry describes early-escape data at or prior to Week 16 as carried forward through Week 28 for the primary outcome. That rule is relevant to interpreting the Week 28 result because it means the endpoint was not simply a Week 28 measurement for every participant. Further details of the early-escape procedure are not reported in the registry record.

3. Trial Design

The registry describes a phase 2, multicenter, randomized, double-blind, placebo-controlled, parallel-group study. It reports triple masking, although the masked roles are not reported in the registry record. The study was marked completed. The registry lists enrollment of 274 participants, with a start in 2012-08 and primary completion in 2013-12.

Five groups are listed: placebo; ustekinumab 90 mg every 8 weeks; ustekinumab 90 mg every 12 weeks; CNTO 1959 200 mg every 8 weeks; and CNTO 1959 50 mg every 8 weeks. Each group is described as being given with methotrexate. Arm-level counts for the primary outcome range from 54 to 55. The registry record does not describe the randomization ratio or give the original planned number of participants for each group.

The primary outcome was the percentage of participants with an ACR 20 response at Week 28. The primary analysis population is described as intent-to-treat, including all randomized participants, and the record states that early-escape data at or prior to Week 16 were carried forward through Week 28. The record does not give further operational details for this rule.

Three secondary outcomes are also posted: change from baseline in DAS28 using CRP at Week 28, ACR 20 response at Week 12, and change from baseline in HAQ-DI at Week 28. The registry lists 16 analyses overall, but the analysis details posted for the primary and secondary outcomes do not establish a complete prespecified statistical plan. The original protocol, planned sample-size justification, and intended handling of multiplicity are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: A total of 274 subjects were enrolled into the study and 273 were treated. One participant in the Ustekinumab 90 milligram (mg) every 8 weeks group did not receive the treatment due to an adverse event before dosing.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The intent-to-treat (ITT) population included all randomized participants. For early escape, data at or prior to Week 16 were carried forward through Week 28.

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: Analysis population included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With American College of Rheumatology 20 (ACR 20) Response at Week 28, measured over Week 28.

The primary endpoint is the percentage of participants who met the ACR 20 response definition at Week 28. In the registry description, a responder needed at least 20 percent improvement from baseline in both tender joint count and swollen joint count, plus improvement in at least 3 of 5 other core measures. Those measures were the participant’s assessment of arthritis pain, the participant’s global assessment of disease activity, the physician’s global assessment of disease activity, physical function measured by HAQ-DI, and CRP.

This endpoint is used to express response as a binary outcome: each participant either meets the response definition or does not. Reporting the percentage gives a readily interpretable summary of how often the threshold was met in each group. It also simplifies comparisons between groups, but it does not show the size or pattern of change for every individual measure. Two participants can both qualify as responders while experiencing different degrees or combinations of improvement.

The Week 28 endpoint is distinct from the Week 12 ACR 20 secondary outcome, and both differ from the continuous DAS28 and HAQ-DI change outcomes. The registry states that the primary analysis used the intent-to-treat population and carried forward early-escape data at or prior to Week 16 through Week 28. The endpoint therefore needs to be understood together with that stated handling rule. Details about other missing primary-outcome data are not reported in the registry record.

7. Results Posted in the Registry

• Ustekinumab 90 mg Every 8 Weeks: 52.7% (29/55) versus 40.0% (22/55) on control; risk difference 12.7 percentage points (95% CI -5.8 to 31.2), risk ratio 1.32 (0.88–1.98); unadjusted two-proportion z-test p = 0.181.
• Ustekinumab 90 mg Every 12 Weeks: 54.5% (30/55) versus 40.0% (22/55) on control; risk difference 14.5 percentage points (95% CI -3.9 to 33.0), risk ratio 1.36 (0.91–2.04); unadjusted two-proportion z-test p = 0.127.
• CNTO1959 200 mg Every 8 Weeks: 44.4% (24/54) versus 40.0% (22/55) on control; risk difference 4.4 percentage points (95% CI -14.1 to 23.0), risk ratio 1.11 (0.72–1.73); unadjusted two-proportion z-test p = 0.639.
• CNTO1959 50 mg Every 8 Weeks: 38.2% (21/55) versus 40.0% (22/55) on control; risk difference -1.8 percentage points (95% CI -20.1 to 16.4), risk ratio 0.95 (0.60–1.52); unadjusted two-proportion z-test p = 0.845.

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.

Change From Baseline in Disease Activity Index Score 28 (DAS28; Using C-reactive Protein [CRP]) Score at Week 28

• 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:
  • Ustekinumab 90 mg Every 8 Weeks: mean -1.52 versus -0.94 on control; difference -0.58 (95% CI -1.08 to -0.08), standardized effect d = -0.44; z-test p = 0.022.
  • Ustekinumab 90 mg Every 12 Weeks: mean -1.49 versus -0.94 on control; difference -0.55 (95% CI -1.04 to -0.06), standardized effect d = -0.42; z-test p = 0.029.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Ustekinumab 90 mg Every 8 Weeks 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 mean is statistically lower for Ustekinumab 90 mg Every 12 Weeks than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With American College of Rheumatology 20 (ACR 20) 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:
  • Ustekinumab 90 mg Every 8 Weeks: 37.0% (20/54) versus 29.1% (16/55) on control; risk difference 7.9 percentage points (95% CI -9.7 to 25.6), risk ratio 1.27 (0.74–2.18); unadjusted two-proportion z-test p = 0.378.
  • Ustekinumab 90 mg Every 12 Weeks: 34.5% (19/55) versus 29.1% (16/55) on control; risk difference 5.5 percentage points (95% CI -11.9 to 22.8), risk ratio 1.19 (0.69–2.06); unadjusted two-proportion z-test p = 0.539.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ustekinumab 90 mg Every 8 Weeks 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 Ustekinumab 90 mg Every 12 Weeks and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Health Assessment Questionnaire - Disability Index (HAQ-DI) Score at Week 28

• 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:
  • Ustekinumab 90 mg Every 8 Weeks: mean -0.48 versus -0.30 on control; difference -0.18 (95% CI -0.38 to 0.02), standardized effect d = -0.33; z-test p = 0.081.
  • Ustekinumab 90 mg Every 12 Weeks: mean -0.44 versus -0.30 on control; difference -0.14 (95% CI -0.34 to 0.06), standardized effect d = -0.26; z-test p = 0.172.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ustekinumab 90 mg Every 8 Weeks 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 Ustekinumab 90 mg Every 12 Weeks and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide several complementary views of response: a continuous disease-activity score, an earlier binary response threshold, and a measure of disability. Taken together, they broaden the description beyond the primary Week 28 responder endpoint. The pattern is not uniform across outcomes or treatment groups, and the secondary results should be viewed as supportive context rather than as a replacement for the primary comparison.

The registry reports selected ANCOVA comparisons for the Week 28 DAS28 and HAQ-DI changes, and Cochran-Mantel-Haenszel comparisons for Week 12 ACR 20 response. The posted results do not include sponsor-reported comparisons for every active group on every secondary endpoint. The available analyses therefore do not form a complete, consistent set of treatment comparisons across all secondary measures.

Unadjusted secondary findings carry less weight because several outcomes and comparisons are examined, creating opportunities for chance findings. The registry record does not state whether a multiplicity adjustment, hierarchical testing plan, or other prespecified strategy was used. Secondary p-values should consequently be read as exploratory evidence unless the full statistical plan establishes otherwise. This is particularly important when a secondary result appears more persuasive than the primary result: outcomes are related, and selectively emphasizing a favorable secondary analysis can exaggerate the apparent consistency of evidence.

The types of measures also differ. A binary response rate records whether a threshold was reached, while continuous change scores retain more gradation in the outcome. Their estimates and p-values are not interchangeable. Baseline-to-follow-up change, model adjustment, missing-data handling, and the timing of measurement can each affect comparisons. The registry record does not report enough detail to determine how every such issue was addressed across the secondary analyses.

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

• Change From Baseline in Disease Activity Index Score 28 (DAS28; Using C-reactive Protein [CRP]) Score at Week 28
• Percentage of Participants With American College of Rheumatology 20 (ACR 20) Response at Week 12
• Change From Baseline in Health Assessment Questionnaire - Disability Index (HAQ-DI) Score at Week 28

9. Statistical Interpretation

10. Statistical Methods Explained

General explanation: A risk difference subtracts the response proportion in one group from the response proportion in another. Positive estimates in these comparisons mean the recorded response proportion was higher in the active-treatment group than in placebo; a negative estimate means it was lower. The risk difference is expressed on the probability scale, so its interval describes uncertainty about the absolute difference between groups. These re-calculations are simple, unadjusted comparisons based on posted group summaries.

The primary endpoint is binary because each participant is classified as meeting or not meeting the ACR 20 criteria. The group percentages summarize those classifications. This approach makes the response rate accessible, but it discards information about how far a participant’s measurements changed beyond the threshold and about participants who improved without reaching it.

General explanation: A confidence interval represents a range of effect estimates compatible with the data and the interval procedure. It conveys both the direction and precision of an estimate. An interval spanning zero does not demonstrate that the groups are identical; it indicates that the data do not pin down the risk difference precisely enough to exclude zero under that procedure. Interpretation should consider the complete interval, not only whether a p-value crosses a conventional threshold.

The sponsor’s posted primary comparisons use the Cochran-Mantel-Haenszel method. The registry gives a p-value for each active-treatment group compared with placebo, but does not post an effect estimate or interval for those analyses. The unadjusted re-calculations use the recorded response counts and group sizes to estimate risk differences and intervals. They are not a reproduction of the sponsor’s full analysis because the registry’s reported method and the simple re-calculations are not identical.

General explanation: The Cochran-Mantel-Haenszel method can combine evidence across strata when a comparison is made while accounting for stratification. The registry record does not identify the strata or give enough detail to reconstruct that analysis. The reported p-values should therefore be read as the registry’s reported inferential results, not as p-values derived from the simple risk-difference calculations.

The secondary continuous outcomes are reported as least-squares means with standard errors. A least-squares mean is a model-based group estimate; it is not necessarily the raw arithmetic average. The registry lists ANCOVA for the reported comparisons of DAS28 and HAQ-DI change. It does not provide the full ANCOVA specifications, including the covariates used, so the adjustment cannot be reconstructed from the record.

General explanation: ANCOVA compares outcome means while adjusting for specified covariates. The adjustment can account for baseline or other prespecified factors and may yield a different estimate or p-value from a simple unadjusted comparison. The exact meaning depends on the model and covariates. Since those details are not reported in the registry record, the sponsor’s ANCOVA results can be described but not independently rebuilt from the posted summaries.

For the continuous outcomes, the re-calculations use estimated pooled standard deviations and give unadjusted mean differences and intervals. The standard deviations are marked as approximate because the registry posts standard errors rather than standard deviations. That distinction matters: a standard error describes uncertainty in a group estimate, while a standard deviation describes participant-level spread. Converting between them requires assumptions about the underlying data and group size; the resulting estimates are therefore approximate rather than exact reconstructions of the participant-level analysis.

General explanation: Over-dispersion occurs when outcomes vary more than a simple statistical model expects. For binary data, extra variation can make standard errors too small if ignored, leading to intervals that are too narrow and p-values that overstate precision. The posted re-calculations do not report an over-dispersion adjustment. The registry’s primary analysis method is Cochran-Mantel-Haenszel, and the record does not specify whether any additional variance adjustments were used.

The planning illustrations use observed effects and stated assumptions to show how participant requirements change under different effect-size scenarios. They are not estimates of the original study design. A planning calculation based on an observed effect is sensitive to the uncertainty in that effect, so it should be used as an illustration rather than a definitive design recommendation. The assumptions and interpretation of those figures are described separately.

Finally, the registry reports several treatment comparisons and several outcomes. Statistical testing across multiple comparisons creates a multiplicity issue: when many hypotheses are assessed, the chance of at least one apparently notable finding can increase if no adjustment or hierarchy is used. The intended strategy for this trial is not reported in the registry record, so the posted p-values should not be assumed to be multiplicity-adjusted.

11. Confidence Intervals and Precision

The primary risk-difference intervals are broad relative to their point estimates. For ustekinumab 90 mg every 8 weeks, the estimate is 0.127 and its interval runs from -0.058 to 0.312. For ustekinumab 90 mg every 12 weeks, the estimate is 0.145, with an interval from -0.039 to 0.330. Both intervals include zero and also allow for positive differences larger than their point estimates.

The intervals for the CNTO 1959 comparisons also include zero. The estimate for 200 mg every 8 weeks is 0.044, with an interval from -0.141 to 0.230. The estimate for 50 mg every 8 weeks is -0.018, with an interval from -0.201 to 0.164. Thus, the posted summaries do not determine the direction of either comparison with much certainty. The uncertainty intervals describe possible effect sizes under the calculation procedure; they are not guarantees about the true value.

The registry record does not state the confidence level for the intervals in the re-calculation, so no confidence percentage is assigned. The sponsor’s primary analyses post p-values but do not include effect estimates or intervals. That leaves less information for judging the magnitude and precision of the sponsor’s estimates than would be available from a reported effect estimate with an interval.

Group sizes for the primary outcome are 54 or 55. With this scale of group size and response percentages, estimates can remain imprecise even when the observed percentages differ. Precision is not the same as whether a comparison is statistically significant: it concerns how narrowly the data constrain the plausible effect. The secondary continuous outcome re-calculations also have intervals, but their procedures and the approximate standard deviations used for those calculations require separate consideration.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are participant counts per arm, not total participants across all groups and not total events. They apply to the two-arm comparison under consideration. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect: 100%, 75%, or 50%. The figures are planning illustrations computed from the observed effect, not the original trial’s design assumptions; those original assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm that the calculation estimates would be needed for an 80% chance of detecting the assumed effect under those planning assumptions, if that effect were the true one. The 90% power column gives the corresponding per-arm count for a 90% chance. Power is a property of a proposed design under specified assumptions, not a measure of what the completed trial achieved.

Across the listed scenarios, planning for a smaller effect requires more participants per arm than planning for the full observed effect. This is expected: smaller differences are harder to distinguish from sampling variation. The calculations also depend strongly on the observed effect, which itself is uncertain, especially when the original groups are small. In comparisons where the observed effect is close to zero, or is negative, resulting planning numbers should not be treated as stable estimates of a future study’s needs.

These values are not observed power. They are illustrations of how sample size changes under the listed assumptions and effect-size scenarios. They do not establish whether the completed study was adequately designed or whether any particular future study would be sufficient.

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 = 0.400; treatment proportion p₁ = 0.527; average p̄ = 0.464.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7052 = 1.3822.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6995 = 0.5887.
4. n = (1.3822 + 0.5887)² / (0.1273)² = 239.8, rounded up to 240 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 <- 0.4                          # control proportion
p1 <- 0.527272727272727                          # 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(1645280)
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 = 240 (80% power), 321 (90% power)
 75% of observed effect: n per arm = 425 (80% power), 569 (90% power)
 50% of observed effect: n per arm = 950 (80% power), 1,272 (90% power)
power.prop.test: 239.8 
Simulated power at n = 240 per arm: 0.799 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparisons using the Cochran-Mantel-Haenszel method. The reported p-values are 0.184 for ustekinumab 90 mg every 8 weeks versus placebo, 0.130 for ustekinumab 90 mg every 12 weeks, 0.642 for CNTO 1959 200 mg every 8 weeks, and 0.832 for CNTO 1959 50 mg every 8 weeks. The registry record does not post effect estimates or intervals for these primary analyses.

The unadjusted re-calculations use the posted response counts and group sizes to estimate risk differences, intervals, and p-values. Their p-values are 0.181, 0.127, 0.639, and 0.845 in the same comparison order. These are close to, but not identical to, the sponsor’s values. The difference is expected when methods differ; the re-calculations do not replace the sponsor’s analysis.

The registry does not flag a discrepancy between the posted results and the simple re-calculations. The sponsor’s reported method remains the primary registry analysis, while the re-calculations offer a transparent, unadjusted view of the group summaries. Since the record does not fully describe the sponsor’s stratification or broader analysis plan, the sponsor’s results cannot be recreated exactly from the posted aggregate data.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists four primary comparisons against a shared placebo group and several secondary outcomes, with 16 analyses overall. Testing several hypotheses raises a multiplicity concern: even when there is no true effect, a larger collection of tests makes it more likely that at least one result may appear notable by chance. This is a general statistical issue, not evidence that any particular posted result is false.

The statistical plan for controlling multiplicity, if any, is not reported in the registry record. It is not possible to determine from the posted results whether the p-values were adjusted, whether testing followed a prespecified hierarchy, or whether the primary comparisons were intended to be interpreted as a family. Accordingly, the p-values should not be described as multiplicity-adjusted, and secondary results warrant particular caution.

The record defines the primary analysis population as intent-to-treat, including all randomized participants. It also states that for early escape, data at or prior to Week 16 were carried forward through Week 28. The registry does not give further details about which observations were carried forward in individual cases, how other missing observations were treated, or whether sensitivity analyses assessed the effect of missing data. Handling missing outcomes can influence a binary response rate, so the stated rule is relevant to interpretation but does not resolve every missing-data question.

The registry names an intent-to-treat population for the primary outcome. Details about analysis populations for every secondary outcome and safety summary are not reported in the registry record. Nor does the record provide enough information to assess adherence to assigned treatment or exclusions from particular analyses. These omissions limit how fully the posted estimates can be connected to the intended protocol analysis.

The record reports randomized allocation and triple masking, but does not describe the masked roles or the randomization procedure. The original statistical analysis plan, sample-size justification, interim analysis plan, and multiplicity strategy are not reported in the registry record. These missing details do not negate the posted results, but they limit independent assessment of whether the analyses followed prespecified decisions.

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: rheumatoid arthritis (6.2%), lobar pneumonia (1.9%), urinary tract infection (1.9%), concussion (1.9%), sciatica (1.9%).

The safety record lists serious adverse events for placebo, the placebo early-escape group, and each active-treatment group. The recorded counts are 3 of 55 for placebo, 1 of 16 for placebo early escape, 4 of 54 for ustekinumab 90 mg every 8 weeks, 3 of 55 for ustekinumab 90 mg every 12 weeks, 3 of 54 for CNTO 1959 200 mg every 8 weeks, and 0 of 55 for CNTO 1959 50 mg every 8 weeks. These are counts of participants affected within the listed groups, not a comparison adjusted for follow-up time or other factors.

The record also lists other adverse events affecting 13 of 55 in placebo, 6 of 16 in placebo early escape, 15 of 54 in ustekinumab 90 mg every 8 weeks, 15 of 55 in ustekinumab 90 mg every 12 weeks, 18 of 54 in CNTO 1959 200 mg every 8 weeks, and 14 of 55 in CNTO 1959 50 mg every 8 weeks. Serious-event terms listed include rheumatoid arthritis at 6.2%, and lobar pneumonia, urinary tract infection, concussion, sciatica, and shock at 1.9% each. Group attribution for these terms is not given in the record.

Deaths are not reported in the registry record. These counts describe the posted safety summaries; they do not by themselves establish comparative safety, especially without details about exposure duration, event definitions, and statistical comparisons.

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

The primary result describes the percentage of participants meeting the registry’s ACR 20 response definition at Week 28 in each group. It does not describe every participant’s degree of change, and it does not establish a causal treatment effect on its own. The risk-difference estimates and intervals are important because they show that the comparisons remain uncertain and include zero.

The primary outcome is one component of a broader record that includes secondary measures and safety summaries. Those outcomes offer additional descriptive information, but the registry’s incomplete reporting of the statistical plan means that secondary p-values should not be treated as independent confirmation. The primary analysis also includes a stated carry-forward approach for early-escape data, and other missing-data details are not reported in the registry record.

The posted results do not show that all regimens have the same effect, nor do they prove that any observed difference is real. An interval that includes zero leaves open a range of possibilities rather than establishing equivalence. Demonstrating equivalence or non-inferiority would require a design and analysis plan aimed at those questions; such aims are not reported in the registry record.

The record also does not establish how results would generalize beyond the studied population or setting. It describes participants with active rheumatoid arthritis despite methotrexate therapy and reports a phase 2 study. Broader applicability cannot be assessed from these aggregate results alone. The appropriate statistical reading is therefore bounded: the registry reports group-level outcomes and sponsor analyses, while the comparisons are imprecise and key protocol and analysis details are not reported.

18. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the distinction between a difference in observed percentages and a precise estimate of a group difference. The Week 28 response percentages vary across the five groups, but the unadjusted intervals for the active-treatment comparisons all include zero. Looking only at the percentages would miss the uncertainty associated with the modest group sizes.

It also illustrates why the analysis method matters. The registry’s primary tests use Cochran-Mantel-Haenszel analyses, while simple re-calculations from the posted counts give slightly different p-values. The distinction is modest in these results, but it is important to label the sponsor’s analysis and the unadjusted calculation correctly rather than treating them as interchangeable.

The multiple active-treatment comparisons, multiple outcomes, early-escape handling, and incomplete reporting of multiplicity and missing-data plans make statistical context especially important. These considerations do not determine the direction of the results, but they affect how confidently individual estimates can be interpreted and how much weight should be placed on secondary findings.

Finally, the planning illustrations demonstrate how requirements change when the target effect is made smaller. They are useful for understanding design sensitivity, but they are not evidence about the trial’s original design or its achieved power. Together, these features make the record a practical example of why effect estimates, uncertainty, analysis methods, and prespecification all matter alongside reported p-values.

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 provides aggregate results rather than participant-level data. Independent reconstruction of the sponsor’s analyses is therefore limited, particularly because the record does not identify the strata used for the primary Cochran-Mantel-Haenszel analyses or the covariates in the ANCOVA models. The primary sponsor analyses post p-values but not effect estimates and intervals.

The primary group sizes are 54 or 55, and the resulting comparisons have broad uncertainty intervals. This limits precision, even where the recorded percentages differ. The four comparisons also use a shared placebo group, so they are related rather than independent pieces of evidence.

The registry record does not report the original sample-size justification, the full prespecified analysis plan, multiplicity handling, the interim analysis plan, or detailed missing-data sensitivity analyses. The primary outcome’s early-escape carry-forward rule is stated, but its implementation and the handling of other missing observations are not described. The original allocation ratio and masked roles are also not reported.

Some secondary continuous-outcome re-calculations use approximate standard deviations derived from posted standard errors. They are not exact reconstructions of participant-level variation. Also, the registry does not report sponsor comparisons for every treatment group on every secondary measure, so the available secondary evidence is incomplete across the full set of arms and endpoints.

The safety summaries give counts but do not provide exposure-adjusted comparisons in the information. Deaths are not reported in the registry record. These limits mean that the safety figures should be treated as descriptive registry summaries, not as a complete comparative safety analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of the Effectiveness and Safety of Ustekinumab (STELARA) and CNTO 1959 Administered Under the Skin of Patients With Active Rheumatoid Arthritis, Despite Existing Methotrexate Therapy — NCT01645280.
• Registry record last updated 2016-05-12; status last verified 2016-05.
• Results first posted 2014-12-19.
• 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

The registry describes a completed, randomized, triple-masked, parallel-group phase 2 study in participants with active rheumatoid arthritis despite methotrexate therapy. Enrollment was 274. The five listed groups received placebo, two ustekinumab regimens, or two CNTO 1959 regimens, each with methotrexate.

The primary endpoint was Week 28 ACR 20 response. The posted response percentages ranged from 38.2 to 54.5 across the groups, and all four unadjusted risk-difference intervals for comparisons with placebo included zero. The sponsor’s reported primary analyses used the Cochran-Mantel-Haenszel method.

Three secondary outcomes and safety summaries are also posted. Important details—including the multiplicity strategy, original sample-size justification, full analysis plan, and several aspects of missing-data handling—are not reported in the registry record. The primary comparisons are therefore best read as uncertain estimates, with secondary and safety findings interpreted in light of the record’s reporting limits.