An Efficacy And Safety Study Evaluating Tofacitinib With And Without Methotrexate Compared To Adalimumab With Methotrexate: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for An Efficacy And Safety Study Evaluating Tofacitinib With And Without Methotrexate Compared To Adalimumab With Methotrexate (NCT02187055), a randomized phase 4 study. The primary outcome is Percentage of Participants Achieving American College of Rheumatology Criteria 50% Improvement (ACR50) Response at Month 6.

2. Clinical Question

The trial examined whether ACR50 response at Month 6 differed among three treatment strategies for people with moderately to severely active rheumatoid arthritis: tofacitinib 5 mg twice daily alone, tofacitinib 5 mg twice daily with methotrexate, and adalimumab 40 mg with methotrexate. It also set out to compare the two tofacitinib strategies with one another and to assess other health outcomes, safety, tolerability, and safety of zoster vaccination before treatment initiation.

3. Trial Design

This was a randomized, parallel-group phase 4 study. The registry record lists quadruple masking, but does not identify which roles were masked or describe how masking was maintained. It reports enrollment of 1152 participants and three treatment groups: tofacitinib 5 mg twice daily, tofacitinib 5 mg twice daily with methotrexate, and adalimumab 40 mg with methotrexate. The record describes the first two as drug interventions and the adalimumab treatment as a biological intervention.

The primary outcome was the percentage of participants achieving ACR50 response at Month 6. The stated primary analysis population was the full analysis set, defined as randomized participants who received at least one dose of the randomized investigational drug. The primary outcome group counts were 384 for tofacitinib alone, 376 for tofacitinib with methotrexate, and 386 for adalimumab with methotrexate. Outcome-specific counts can differ from the overall arm counts; the registry record does not explain all such differences.

The trial also assessed changes in disease-activity scores and remission outcomes at Month 6, along with safety and tolerability. The listed secondary outcomes include SDAI, CDAI, and DAS28-4 measures, as well as remission criteria. The brief summary additionally describes assessment of the safety of zoster vaccination before treatment initiation.

The registry record gives the trial status as completed and lists start and primary-completion dates. It does not report the rationale for the original enrollment target, the original sample-size assumptions, details of randomization procedures, or a full statistical analysis plan. The specific masking roles, treatment adherence information, and duration of safety follow-up are also 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: Although a total of 1,152 participants were randomized, only 1,146 participants received treatment and are included in the full analysis set summarized below.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) included all participants who were randomized and received at least one dose of the randomized investigational drug (tofacitinib or adalimumab).

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 American College of Rheumatology Criteria 50% Improvement (ACR50) Response at Month 6, measured over Month 6.

The primary endpoint was the percentage of participants achieving American College of Rheumatology Criteria 50% Improvement, or ACR50, at Month 6. It is a binary outcome: each participant either meets the response criteria or does not, and the group result is expressed as a percentage of participants.

As defined in the registry record, ACR50 requires at least 50% improvement in tender joint count or swollen joint count and 50% improvement in three of five additional measures: the physician’s global assessment of disease activity, the participant’s global assessment, the participant’s assessment of pain, functional disability measured by a health assessment questionnaire, and C-reactive protein. The outcome therefore combines joint findings with assessments of disease activity, pain, function, and inflammation rather than relying on a single measure.

In general, a composite response criterion can summarize change across several aspects of a condition, but its result depends on the precise criteria and assessment time point. The Month 6 endpoint gives a defined time for comparing response proportions across the randomized groups. It does not, by itself, describe every participant’s experience, the size of change among people who did not meet the response threshold, or longer-term outcomes. Those questions require other outcomes and follow-up information.

7. Results Posted in the Registry

• Tofacitinib 5 mg BID + MTX: 46.0% (173/376) versus 38.3% (147/384) on control; risk difference 7.7 percentage points (95% CI 0.7 to 14.7), risk ratio 1.20 (1.02–1.42); unadjusted two-proportion z-test p = 0.031.
• Adalimumab 40 mg + MTX: 43.8% (169/386) versus 38.3% (147/384) on control; risk difference 5.5 percentage points (95% CI -1.4 to 12.4), risk ratio 1.14 (0.96–1.36); unadjusted two-proportion z-test p = 0.121.

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 Simplified Disease Activity Index (SDAI) Value at Month 6

• 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:
  • Tofacitinib 5 mg BID + MTX: mean -26.60 versus -23.70 on control; difference -2.90 (95% CI -4.62 to -1.18), standardized effect d = -0.25; z-test p = <0.001.
  • Adalimumab 40 mg + MTX: mean -25.60 versus -23.70 on control; difference -1.90 (95% CI -3.62 to -0.18), standardized effect d = -0.16; z-test p = 0.030.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Tofacitinib 5 mg BID + MTX 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 Adalimumab 40 mg + MTX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Clinical Disease Activity Index (CDAI) Value at Month 6

• 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:
  • Tofacitinib 5 mg BID + MTX: mean -25.50 versus -22.90 on control; difference -2.60 (95% CI -4.29 to -0.91), standardized effect d = -0.23; z-test p = 0.003.
  • Adalimumab 40 mg + MTX: mean -24.80 versus -22.90 on control; difference -1.90 (95% CI -3.59 to -0.21), standardized effect d = -0.17; z-test p = 0.028.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Tofacitinib 5 mg BID + MTX 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 Adalimumab 40 mg + MTX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Disease Activity Score 28-4 (DAS28-4) Including CRP at Month 6

• 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:
  • Tofacitinib 5 mg BID + MTX: mean -2.50 versus -2.10 on control; difference -0.40 (95% CI -0.59 to -0.21), standardized effect d = -0.31; z-test p = <0.001.
  • Adalimumab 40 mg + MTX: mean -2.30 versus -2.10 on control; difference -0.20 (95% CI -0.39 to -0.01), standardized effect d = -0.15; z-test p = 0.043.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Tofacitinib 5 mg BID + MTX 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 Adalimumab 40 mg + MTX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the assessment beyond whether participants crossed the ACR50 response threshold. The registry record lists changes in SDAI, CDAI, DAS28-4 including CRP and ESR, and several remission outcomes. It reports 30 secondary outcome measures. Numerical results available for SDAI, CDAI, and DAS28-4 including CRP show more negative average changes in both combination-treatment groups than in the tofacitinib-alone group. This is a directional pattern in these disease-activity measures, not a replacement for the primary endpoint or proof that the treatments differ in a clinically important way.

For the three continuous outcomes with numerical results, the sponsor-reported comparisons against tofacitinib alone are consistent with larger reductions in the combination groups. These outcomes can help describe changes in disease activity that the binary ACR50 response does not capture. They do not resolve the primary analysis questions: they have different scales, different outcome definitions, and their own analysis uncertainties. Nor should multiple secondary findings be treated as independent confirmations of a single primary conclusion.

In general, when many outcomes and comparisons are examined, the chance of obtaining apparently notable results by chance increases unless the analysis accounts for multiplicity. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for secondary outcomes. Accordingly, unadjusted secondary results carry less inferential weight than a prespecified primary result with a fully described analysis plan. Their value is mainly to describe the range and direction of recorded outcomes and to identify questions that may merit further investigation, rather than to establish multiple definitive treatment differences.

Some listed secondary outcomes do not have numerical summaries in the record details used for this explanation. Their results and any associated uncertainty are not reported in the registry record in the information available for interpretation. The overall secondary pattern should therefore be understood as limited to the outcome summaries that are reported, rather than assumed to apply to every listed outcome.

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

• Change From Baseline in Simplified Disease Activity Index (SDAI) Value at Month 6
• Change From Baseline in Clinical Disease Activity Index (CDAI) Value at Month 6
• Change From Baseline in Disease Activity Score 28-4 (DAS28-4) Including CRP at Month 6
• Change From Baseline in Disease Activity Score 28-4 (DAS28-4) Including Erythrocyte Sedimentation Rate (ESR) at Month 6
• Percentage of Participants Achieving Observed American College of Rheumatology-European League Against Rheumatism (ACR-EULAR) Boolean Remission Criteria at Month 6
• Percentage of Participants Achieving SDAI ≤3.3 at Month 6
• Percentage of Participants Achieving CDAI ≤2.8 at Month 6
• Percentage of Participants Achieving DAS28-4 (ESR) <2.6 at Month 6

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a response proportion, so the basic descriptive statistic is the percentage of participants meeting ACR50 criteria in each treatment group. The posted values are 38.28% for tofacitinib alone, 46.01% for tofacitinib with methotrexate, and 43.78% for adalimumab with methotrexate. The primary analysis population is the full analysis set defined in the registry record. The outcome-specific counts are reported for each group, but further details about handling participants without an observed Month 6 assessment are not reported in the registry record.

What does a risk difference describe?

In general, a risk difference subtracts one group’s event proportion from another’s. For a response outcome, it expresses the difference in the percentage achieving the response, in percentage-point terms when expressed as a percentage. Its sign depends on the order in which the groups are compared. A positive or negative value is not meaningful without knowing that order. The sponsor’s reported comparisons specify group order and report differences in response rate; the recalculated comparisons use a different stated reference orientation. These estimates should not be treated as interchangeable when their signs or analysis methods differ.

The simple recalculations are unadjusted comparisons based on the posted summary statistics. They do not replace the sponsor’s analysis, which is especially important because a discrepancy is flagged between the recalculation and the sponsor-reported results. The sponsor’s own analysis takes precedence. The registry record identifies the sponsor analyses as normal approximations to proportions for the primary comparisons. It does not report the full details needed to reproduce every aspect of those analyses.

How should the comparison type be read?

The sponsor results are labelled non-inferiority or equivalence analyses. In general, a non-inferiority assessment asks whether an outcome for one treatment is not worse than another by more than a prespecified margin; an equivalence assessment asks whether a difference is contained within prespecified bounds. The margin or bounds are essential to interpreting such a test. They are not reported in the registry record. A confidence interval and a p-value alone do not reveal the chosen margin, whether a prespecified criterion was met, or how the analysis handled departures from the planned population.

The reported confidence intervals are 98.34% intervals for the primary comparisons. In general, a confidence interval gives a range of estimates compatible with the observed data under the statistical model and its assumptions. The width reflects statistical precision: wider intervals leave more uncertainty about the size and direction of the difference. A confidence interval that includes zero does not establish that the treatments are identical; it indicates that a zero difference is compatible with that interval under the stated analysis. For a non-inferiority question, the relation of the interval to the margin—not just whether it crosses zero—is central.

What do the secondary continuous outcomes add?

For SDAI, CDAI, and DAS28-4 including CRP, the registry record gives least-squares mean changes from baseline at Month 6, with standard errors. These are continuous outcomes rather than response proportions. In general, a mean change describes the average change on the outcome scale, while a standard error describes uncertainty in the estimated mean. A least-squares mean is an estimated mean from a statistical model; the registry record does not provide enough detail to reconstruct all model terms or assumptions. The recalculated mean differences are unadjusted approximations from the reported summary statistics and should not be mistaken for the sponsor’s model-based comparison.

For the primary and secondary comparisons, the registry record does not report a complete account of the covariate adjustment, missing-data assumptions, multiplicity strategy, or sensitivity analyses. It also does not report the full analysis code or model specifications. These omissions limit independent assessment of how robust the reported inferences are to alternative analytical choices.

Why does over-dispersion matter in general?

For a binary outcome, a basic statistical model may assume that variation in the observed response counts is fully described by the assumed event probabilities and group sizes. In general, over-dispersion means that the data vary more than that model expects. If present and not accounted for, uncertainty can be understated, making intervals too narrow and tests too optimistic. The registry record does not report an over-dispersion assessment for the primary outcome, so it is not possible to say whether it was relevant or how it was handled in the sponsor analysis.

These methods explain how to read the posted estimates, not a complete reconstruction of the trial’s analysis. The original statistical plan, its decision rules, and the treatment of missing observations are not reported in the registry record.

11. Confidence Intervals and Precision

The sponsor’s primary comparisons have 98.34% confidence intervals. For tofacitinib alone compared with tofacitinib plus methotrexate, the reported difference in response rate was -7.73 and the interval ranged from -16.29 to 0.83. For tofacitinib alone compared with adalimumab plus methotrexate, the reported difference was -5.50, with an interval from -13.98 to 2.98. For the two combination groups, the reported difference was 2.23, with an interval from -6.40 to 10.86. Each interval includes zero, so the sponsor-reported interval estimates allow uncertainty about the direction of the difference.

In general, an interval’s width conveys precision: a narrower interval constrains the plausible values more tightly, while a wider interval allows a broader range. Precision is not the same as clinical importance. An interval may be statistically informative without showing whether a difference would matter to patients, and the registry record does not state a clinically important threshold for the ACR50 comparison.

The sponsor’s intervals are not the same as the simple unadjusted recalculations. Since a discrepancy is flagged, the sponsor’s own analysis takes precedence for interpretation. The registry record does not include the non-inferiority margin, so the intervals cannot by themselves establish whether a specified non-inferiority criterion was met. The arm percentages also have no arm-specific confidence intervals reported in the primary outcome record.

For the secondary continuous outcomes, the record reports standard errors for the group least-squares means and sponsor-reported 95% intervals for selected differences. These quantify uncertainty under their respective analyses. They do not account for every source of uncertainty, such as potential bias from missing outcomes or the consequences of examining multiple outcomes. Those issues depend on the analysis plan and data-handling choices, which are not fully reported in the registry record.

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 expressed as participants per arm for 80% power and participants per arm for 90% power. They are not total-event counts. For the primary comparison of tofacitinib alone with tofacitinib plus methotrexate, the illustration based on 100% of the observed effect gives 640 participants per arm for 80% power and 856 participants per arm for 90% power. The smaller-effect scenarios require more participants per arm: planning for 75% of the observed effect gives 1,131 for 80% power and 1,513 for 90% power, while planning for 50% gives 2,526 and 3,381, respectively.

In general, the 80% and 90% columns describe the probability, under the stated planning assumptions and if the assumed effect is true, of detecting that effect according to the chosen test criterion. The 90% target is more demanding than the 80% target and therefore requires more participants in these illustrations. Smaller effects are harder to distinguish from random variation, so the illustrations show that they need larger per-arm sample sizes.

The stated assumptions for these planning illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect equal to the stated fraction of the observed effect. These figures are planning illustrations calculated from the observed effect, not the trial’s original design calculations. The trial’s own design assumptions and sample-size justification are not reported in the registry record. These figures are not observed power and should not be read as a retrospective measure of how likely the trial was to find its observed result.

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 = 0.383; treatment proportion p₁ = 0.460; average p̄ = 0.421.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6983 = 1.3687.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6962 = 0.5859.
4. n = (1.3687 + 0.5859)² / (0.0773)² = 639.5, rounded up to 640 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 <- 0.3828125                          # control proportion
p1 <- 0.460106382978723                          # 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(2187055)
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 = 640 (80% power), 856 (90% power)
 75% of observed effect: n per arm = 1,131 (80% power), 1,513 (90% power)
 50% of observed effect: n per arm = 2,526 (80% power), 3,381 (90% power)
power.prop.test: 639.5 
Simulated power at n = 640 per arm: 0.800 (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 analyses are the primary reference for the trial’s reported comparisons. The registry record flags a discrepancy between those analyses and the simple unadjusted recalculations from the posted summary statistics, so the sponsor’s own analysis takes precedence. The recalculations are useful as a separate check on the relationship between the arm-level summaries, but they are not substitutes for the sponsor’s analysis or its stated inferential framework.

For the primary outcome, the sponsor reports differences in response rate with 98.34% confidence intervals and labels the analyses as non-inferiority or equivalence. For tofacitinib alone versus tofacitinib with methotrexate, the reported difference is -7.73, with an interval from -16.29 to 0.83. For tofacitinib alone versus adalimumab with methotrexate, it is -5.50, with an interval from -13.98 to 2.98. For tofacitinib with methotrexate versus adalimumab with methotrexate, it is 2.23, with an interval from -6.40 to 10.86.

The record does not report the non-inferiority margin or enough of the statistical plan to independently assess the formal decision rule. Therefore, it is appropriate to describe the sponsor’s reported estimates and analysis labels, but not to infer that a non-inferiority or equivalence criterion was satisfied solely from the information recorded. Where the recalculated and sponsor-reported results diverge, interpretation should follow the sponsor analysis while recognizing that the missing analysis details limit independent verification.

15. Multiplicity, Missing Data and Analysis Populations

The registry record describes one primary endpoint, ACR50 response at Month 6, and lists a broad set of secondary outcomes. It does not report whether testing across the treatment comparisons and secondary outcomes was controlled through a multiplicity procedure, an ordered testing strategy, or another prespecified approach. Without that information, the nominal evidence from multiple unadjusted comparisons should not be interpreted as if each were the only test conducted.

In general, multiplicity matters because repeated testing can increase the chance of at least one result appearing notable by chance. A prespecified strategy can determine which comparisons are confirmatory and how uncertainty is interpreted across them. The record does not report that strategy, so the strength of inference across the secondary outcomes cannot be fully assessed. This is one reason to give the primary outcome priority and to treat secondary findings as supportive or exploratory unless their role and multiplicity handling are clear.

The registry record defines the primary analysis population as the full analysis set, including randomized participants who received at least one dose of the randomized investigational drug. It does not provide the complete missing-data rules for the primary outcome or all secondary measures. It does not report how missing Month 6 observations were handled, whether any imputation was used, or what sensitivity analyses were performed to examine alternative assumptions. These details matter because a response rate can be affected if outcome availability differs across groups or is related to response.

The record also does not report a complete statistical analysis plan, the non-inferiority margin, or all model specifications and decision rules. It is therefore not possible to establish from the registry record alone whether all analysis choices were prespecified or how deviations, if any, were addressed. These are limits on assessing robustness and reproducibility; they do not, by themselves, show that the analysis was inappropriate.

Finally, the registry record does not report interim-analysis procedures or stopping rules. Their presence or absence should not be inferred. The interpretation remains bounded by the reported population definition, outcome summaries, sponsor comparisons, and the important methodological details that are not reported in the registry record.

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: hip fracture (0.8%), cellulitis (0.8%), pyelonephritis (0.5%), chest pain (0.5%), cholelithiasis (0.5%).

The registry record reports counts of participants with serious adverse events and counts with other adverse events for each group. For tofacitinib alone, the serious adverse-event count was 35 among 384 participants at risk, and the other adverse-event count was 51 among 384 at risk. For tofacitinib with methotrexate, the corresponding counts were 27 among 376 and 72 among 376. For adalimumab with methotrexate, they were 24 among 386 and 69 among 386.

These are recorded counts, not adjusted comparisons. No comparative statistical analysis of these safety counts is reported in the record details used for this explanation. The registry also lists serious adverse-event terms including hip fracture and cellulitis at 0.8% each, and pyelonephritis, chest pain, cholelithiasis, and pyrexia at 0.5% each. The record does not identify these percentages by treatment group in the information, so they should not be assigned to a specific group.

In general, adverse-event counts need context, including follow-up duration, definitions, severity, and how events were collected. The duration of safety follow-up and detailed event-handling methods are not reported in the registry record. Death counts are not reported. These data describe recorded events during the study; they do not alone establish comparative safety or explain the cause of any event.

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

The primary outcome describes the percentage of participants meeting a defined ACR50 response criterion at Month 6. The observed values were 38.28% for tofacitinib alone, 46.01% for tofacitinib with methotrexate, and 43.78% for adalimumab with methotrexate. The sponsor’s reported comparisons provide estimates and 98.34% confidence intervals, but each interval includes zero. Because the record labels these as non-inferiority or equivalence analyses while not reporting the margin, those results cannot be independently translated into a formal conclusion about meeting the relevant decision criterion.

The descriptive percentages do not establish that one treatment works or does not work. They do not show what would have happened to the same participants under another treatment, nor do they describe every aspect of disease activity, quality of life, or longer-term outcomes. ACR50 is a threshold-based composite outcome; participants who fall short of the threshold may still have experienced change, and those who meet it may have different patterns of change across its components.

The secondary disease-activity summaries add context, but they have separate scales and analyses. Their interpretation is limited by unreported multiplicity procedures and incomplete detail on missing-data handling and model assumptions. The adverse-event counts describe events recorded in each group but do not, on their own, quantify comparative risk over a specified follow-up period. No death counts are reported.

In general, a trial estimate is most informative when considered with its uncertainty, outcome definition, analysis population, and design. The registry record gives useful arm-level response percentages and sponsor-reported comparisons, but it does not report all information needed to independently reproduce the statistical analysis or judge the non-inferiority margin. These limitations call for a careful, bounded interpretation rather than a broad claim about comparative treatment effects.

18. Why This Trial Matters Statistically

This trial raises several statistical issues that are common in randomized clinical research. It compares three strategies, includes both a monotherapy-versus-combination question and comparisons with an active treatment, and uses a threshold-based binary primary outcome. The interpretation depends not only on the observed response percentages but also on the order of comparisons, the confidence intervals, and the type of inferential question being asked.

In particular, non-inferiority and equivalence claims require prespecified margins. A confidence interval crossing zero does not answer whether a non-inferiority margin has been met, and the margin is not reported in the registry record. This makes the distinction between descriptive response percentages, simple unadjusted recalculations, and the sponsor’s formal analysis important. The record flags a discrepancy, so the sponsor’s analysis takes precedence while the missing analysis details remain relevant to independent review.

The secondary outcomes also illustrate why multiplicity matters. Multiple measures can offer a richer view of disease activity, but they do not each carry the same confirmatory weight as a designated primary outcome. The record’s incomplete information on multiplicity and missing-data methods limits how strongly the secondary pattern can be interpreted.

Finally, the sample-size illustrations help distinguish observed study results from planning calculations. They are based on the observed effect and stated hypothetical assumptions, not the trial’s original design justification. They do not provide observed power. Together, these points show why statistical interpretation requires attention to estimand, analysis population, uncertainty, prespecification, and the limits of the registry record—not only to the arm-level percentages.

19. Limitations

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

Several trial-specific limitations affect interpretation. The registry record does not report the non-inferiority margin or the complete decision rules for the sponsor’s non-inferiority or equivalence analyses. Although sponsor-reported differences and confidence intervals are available, the omitted margin prevents independent assessment of the formal criterion. A discrepancy is flagged between sponsor results and simple unadjusted recalculations, making it especially important to distinguish the two; the sponsor’s analysis takes precedence.

The full statistical analysis plan is not reported. In particular, the record does not describe a multiplicity strategy across the several primary comparisons and many secondary outcomes. It does not fully state how missing Month 6 measurements were handled, whether imputation was used, or what sensitivity analyses were undertaken. The model specifications for the least-squares means and details of any covariate adjustment are also not reported.

The primary analysis population is defined, but the reasons for outcome-specific differences in reported group counts are not described. The registry record does not provide sufficient detail to assess the effect of incomplete outcome data or treatment discontinuation on the estimates. Likewise, detailed adherence information and the duration of safety follow-up are not reported, limiting assessment of exposure and event context.

The adverse-event information consists of recorded counts and selected event terms; it does not include a comparative safety model or reported death counts. The record also does not give the original sample-size justification, so the planning illustrations based on observed effects cannot establish what assumptions informed the trial’s design. These omissions constrain independent evaluation; they should not be treated as evidence that a particular analysis or result is wrong.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: An Efficacy And Safety Study Evaluating Tofacitinib With And Without Methotrexate Compared To Adalimumab With Methotrexate — NCT02187055.
• Registry record last updated 2018-06-27; status last verified 2018-05.
• Results first posted 2018-06-27.
• 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 record describes a completed randomized, quadruple-masked, parallel-group phase 4 trial with enrollment of 1152 participants with moderately to severely active rheumatoid arthritis. It compared tofacitinib 5 mg twice daily alone, the same tofacitinib regimen with methotrexate, and adalimumab 40 mg with methotrexate.

The primary outcome was ACR50 response at Month 6. Recorded response percentages were 38.28%, 46.01%, and 43.78%, respectively. Sponsor-reported comparisons were labelled non-inferiority or equivalence analyses, but the margin is not reported. A discrepancy with simple unadjusted recalculations is flagged, so the sponsor’s own analysis takes precedence.

The record also includes secondary disease-activity outcomes and adverse-event counts. Important details—including the complete statistical plan, multiplicity strategy, missing-data methods, and original sample-size justification—are not reported in the registry record. These gaps limit independent assessment of the reported comparisons.