Efficacy and Safety of GSK3196165 Versus Placebo and Tofacitinib in Participants With Moderately to Severely Active Rheumatoid Arthritis Who Have an Inadequate Response to Methotrexate: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of GSK3196165 Versus Placebo and Tofacitinib in Participants With Moderately to Severely Active Rheumatoid Arthritis Who Have an Inadequate Response to Methotrexate (NCT03980483), a randomized phase 3 study. The primary outcome is Percentage of Participants Achieving 20 Percentage (%) Improvement in American College of Rheumatology Criteria (ACR20) at Week 12 Superiority Comparison With Placebo.

2. Clinical Question

The clinical question is about a short-term measure of response, not every aspect of rheumatoid arthritis or the full treatment period. ACR20 combines changes in joint counts with changes in several patient, clinician, functional, and inflammatory measures. The Week 12 placebo comparison therefore addresses whether the recorded proportion meeting that composite response definition differed between randomized groups at that assessment. It does not, by itself, describe durability, longer-term outcomes, or the balance of benefits and harms.

3. Trial Design

The registry describes a randomized, double-blind, parallel-group phase 3 study at multiple centres. Enrollment was 1537. The study evaluated GSK3196165 with methotrexate in adults with moderately to severely active rheumatoid arthritis and an inadequate response to methotrexate. The listed study dates run from 2019-05-16 to primary completion on 2021-09-15, and the record marks the study completed.

The treatment period was 52 weeks, following a screening phase of up to 6 weeks. Participants were assigned to weekly subcutaneous GSK3196165 90 mg or 150 mg, tofacitinib 5 mg twice daily, or placebo, with methotrexate. Three placebo groups were included: participants received placebo for 12 weeks, then switched to an active treatment through Week 52. For analyses through Week 12, the placebo groups were pooled as a reference. The registry describes an allocation ratio of 6:6:3:1:1:1 across the listed treatment assignments.

The posted primary outcome is the percentage achieving ACR20 at Week 12, with a superiority comparison against placebo. Secondary outcomes include a low disease activity measure, change in functional disability, later ACR responses, and outcomes for the placebo-switch groups. Some later outcomes address non-inferiority versus tofacitinib. The record lists 98 outcome measures and 7 analyses. The study also collected adverse-event information, including serious adverse events and deaths.

The original sample-size justification and the trial’s full statistical analysis plan are not reported in the registry record. Nor is the registry record a substitute for the full protocol; its public descriptions do not establish all operational details of analysis or follow-up.

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: Analysis of this study were reported for GSK3196165 90mg, GSK3196165 150mg, Tofacitinib 5 mg and all placebo arms are pooled to a single group to serve as reference for comparison of active treatment arms versus Placebo for primary efficacy endpoint analysis at Week 12.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis was performed on the Intent-to-Treat (ITT) set that inlcudes all randomized participants who received at least one dose of study treatment. This population was based on the treatment the participant was randomized to. Analysis was performed using multiple imputation method to handle missing data.

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.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving 20 Percentage (%) Improvement in American College of Rheumatology Criteria (ACR20) at Week 12 Superiority Comparison With Placebo, measured over Week 12.

The primary endpoint is the percentage of participants achieving ACR20 at Week 12. ACR20 is a composite response criterion: it requires a 20% improvement from baseline in both tender joint count and swollen joint count, plus a 20% improvement in three of five additional measures. Those measures cover patient and physician global assessments, pain, physical function measured by HAQ-DI, and an acute-phase inflammatory marker, hsCRP.

A composite endpoint combines information across aspects of disease activity rather than relying on a single symptom or laboratory measurement. Requiring improvement in the joint counts and several additional measures makes the endpoint a structured response definition. It can be useful for comparing the proportion of participants who meet a common threshold at a specified assessment time.

The endpoint is binary at the participant level: each participant either meets the ACR20 criterion or does not. The group result is therefore reported as a percentage. This makes the result interpretable as the proportion meeting the defined threshold, but it does not convey the magnitude of improvement among participants who respond or the pattern of change in each component. The primary endpoint concerns Week 12; it should not be read as a complete description of response over the 52-week treatment period.

7. Results Posted in the Registry

• GSK3196165 90mg + MTX: 54.8% (281/513) versus 42.6% (109/256) on control; risk difference 12.2 percentage points (95% CI 4.8 to 19.6), risk ratio 1.29 (1.09–1.51); unadjusted two-proportion z-test p = 0.001.
• GSK3196165 150mg + MTX: 51.0% (260/510) versus 42.6% (109/256) on control; risk difference 8.4 percentage points (95% CI 1.0 to 15.9), risk ratio 1.20 (1.01–1.41); unadjusted two-proportion z-test p = 0.028.
• Tofacitinib 5mg + MTX: 63.6% (164/258) versus 42.6% (109/256) on control; risk difference 21.0 percentage points (95% CI 12.6 to 29.4), risk ratio 1.49 (1.26–1.77); 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 Achieving Clinical Disease Activity Index (CDAI) Total Score Less Than or Equal to (<=)10 [CDAI Low Disease Activity (LDA)] 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:
  • GSK3196165 90mg + MTX: 20.9% (107/513) versus 14.1% (36/256) on control; risk difference 6.8 percentage points (95% CI 1.3 to 12.3), risk ratio 1.48 (1.05–2.10); unadjusted two-proportion z-test p = 0.022.
  • GSK3196165 150mg + MTX: 19.8% (101/510) versus 14.1% (36/256) on control; risk difference 5.7 percentage points (95% CI 0.3 to 11.2), risk ratio 1.41 (0.99–2.00); unadjusted two-proportion z-test p = 0.050.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for GSK3196165 90mg + MTX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GSK3196165 150mg + MTX 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) at Week 12

• 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:
  • GSK3196165 90mg + MTX: mean -0.46 versus -0.27 on control; difference -0.19 (95% CI -0.27 to -0.11), standardized effect d = -0.34; z-test p = <0.001.
  • GSK3196165 150mg + MTX: mean -0.38 versus -0.27 on control; difference -0.11 (95% CI -0.19 to -0.03), standardized effect d = -0.20; z-test p = 0.008.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for GSK3196165 90mg + 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 GSK3196165 150mg + MTX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Achieving 20% Improvement in ACR20 at Week 24 (Non-Inferiority Versus Tofacitinib)

• 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:
  • GSK3196165 150mg + MTX: 61.4% (313/510) versus 63.9% (328/513) on control; risk difference -2.6 percentage points (95% CI -8.5 to 3.4), risk ratio 0.96 (0.87–1.06); unadjusted two-proportion z-test p = 0.396.
  • Tofacitinib 5mg + MTX: 74.4% (192/258) versus 63.9% (328/513) on control; risk difference 10.5 percentage points (95% CI 3.7 to 17.2), risk ratio 1.16 (1.06–1.28); unadjusted two-proportion z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between GSK3196165 150mg + MTX 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 Tofacitinib 5mg + MTX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary question to disease activity, physical function, and response at later assessments. The registry includes a Week 12 low disease activity measure, change in HAQ-DI, later ACR response outcomes, and outcomes for groups that began on placebo before switching to active treatment. It also lists comparisons addressing non-inferiority versus tofacitinib. Together, these outcomes describe a broader set of response dimensions and time points than the primary endpoint alone.

In broad terms, the posted secondary results include differences between active treatment groups and placebo on some Week 12 measures, while the later ACR results also permit comparisons between active treatment groups. This overall pattern is related to the primary Week 12 ACR20 result, but the endpoints are not interchangeable. ACR response, low disease activity, and HAQ-DI capture different definitions or aspects of outcome, and later assessments involve different time points and, for some groups, a treatment switch.

Secondary outcomes generally carry less inferential weight when many outcomes and comparisons are examined without a reported multiplicity procedure. Each additional test creates another opportunity for a nominally notable result to occur by chance. The registry record does not report a complete multiplicity strategy for the secondary family, and the displayed recalculations are unadjusted. These secondary findings should therefore be treated as supportive or exploratory rather than as independent confirmation of the primary result.

Non-inferiority questions require a prespecified margin and a decision rule that accounts for the interval around the treatment contrast. The registry reports non-inferiority analysis labels for selected Week 24 comparisons, but the margin and full decision framework are not reported in the registry record. The label alone is not enough to verify the conclusion or compare it with the Week 12 superiority question.

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

• Percentage of Participants Achieving Clinical Disease Activity Index (CDAI) Total Score Less Than or Equal to (<=)10 [CDAI Low Disease Activity (LDA)] at Week 12
• Change From Baseline in Health Assessment Questionnaire Disability Index (HAQ-DI) at Week 12
• Percentage of Participants Achieving 20% Improvement in ACR20 at Week 24 (Non-Inferiority Versus Tofacitinib)
• Percentage of Participants Achieving 50%/70% Improvement in American College of Rheumatology Criteria (ACR50/70) at Week 24 and ACR 20/50/70 at and Week 52 for Treatment Arms Who Started Study Intervention From Day 1
• Percentage of Participants Achieving ACR20/50/70 at Week 24 and Week 52 for Placebo Switched Arms
• Percentage of Participants Achieving CDAI Total Score <=10 (CDAI LDA) at Week 24 and Week 52 for Treatment Arms Who Started Study Intervention From Day 1
• Percentage of Participants Achieving CDAI Total Score <=10 (CDAI LDA) at Week 24 and Week 52 for Placebo Switched Arms
• Percentage of Participants Achieving CDAI Total Score <=2.8 (CDAI Remission) at Week 12

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because each participant either meets the ACR20 response definition at Week 12 or does not. An arm-level percentage expresses the frequency of that response in the analyzed group. The risk difference is an absolute comparison between two such proportions. It is reported in the recalculations as a proportion, so values such as 0.122 should be read as a difference on the probability scale, not as an odds ratio. The interval around a risk difference conveys uncertainty about the estimated group contrast.

A risk difference answers a different question from a relative measure. It describes the absolute separation between the observed response proportions, whereas a risk ratio compares the proportions multiplicatively and an odds ratio compares the odds. These measures need not have the same numerical value or interpretation. In particular, an odds ratio is not itself a percentage-point difference, and it should not be described as a direct multiplier of the probability of response. The registry’s sponsor-reported primary analyses use logistic regression and report odds ratios. The recalculated comparisons use posted event counts and denominators and are simple, unadjusted summaries.

Logistic regression is a model commonly used when an outcome has two possible values. It models the log odds of the event and can produce an odds ratio for a treatment comparison. The posted sponsor analysis identifies logistic regression, but the registry record does not report enough detail to reconstruct the full model specification, including all covariates or other adjustments. The sponsor’s reported model estimates should therefore be read as the trial analysis, not treated as interchangeable with the basic risk-difference recalculations.

A confidence interval gives a range of estimates compatible with the data and the stated analysis under its assumptions. It is a measure of precision, not a guarantee that the true effect lies in the displayed range, nor a probability statement about a particular treatment. For the recalculated comparisons, an interval that does not include the null value of no risk difference is consistent with evidence of a difference under the unadjusted method. That observation does not incorporate any unreported multiplicity adjustment or replace the sponsor’s specified analysis. The reported sponsor intervals accompany odds ratios, whose null value is one rather than zero.

A p-value measures how unusual data at least as discrepant as those observed would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The recalculated p-values are explicitly unadjusted. The registry also reports sponsor p-values for the logistic-regression comparisons. Since the primary outcome involves several treatment comparisons and the study reports many secondary outcomes, unadjusted p-values should not be read as if they account for every comparison.

The analysis population is described as the intent-to-treat set, including randomized participants who received at least one dose, with participants analyzed according to randomized treatment. The registry says multiple imputation was used to handle missing data, but the available description is truncated and does not report the imputation model, assumptions, or sensitivity analyses. Multiple imputation is a general approach that replaces missing values with repeated plausible values based on an analysis model, then combines the resulting estimates to reflect uncertainty from missingness. Its validity depends on assumptions and on the suitability of the model; the registry record does not permit a detailed assessment of those aspects.

For secondary continuous outcomes, the posted values may be least-squares means with standard errors, while the simple recalculations use mean differences. A standard error describes the estimated sampling uncertainty of a mean, whereas a standard deviation describes variability among individual observations. These are not interchangeable. In the HAQ-DI comparison, the recalculation notes that the pooled standard deviation is approximate, based on the posted standard errors. The trial’s reported model details for these secondary comparisons are not listed in the available record.

General statistical context: randomization supports a fair comparison by allocating participants to groups without relying on treatment choice, while blinding can reduce some influences on assessment and participant reporting. Neither feature removes uncertainty, missing-data concerns, or the consequences of testing many outcomes. Over-dispersion is a general issue when observed variability exceeds what a simple model assumes; it can make standard errors too small if ignored. The registry information for the primary binary outcome does not report an over-dispersion adjustment, so no such method should be inferred.

11. Confidence Intervals and Precision

The Week 12 recalculated risk-difference intervals provide a sense of precision for the unadjusted comparisons with pooled placebo. For GSK3196165 90 mg, the interval is 0.048 to 0.196. For 150 mg, it is 0.009 to 0.159. For tofacitinib, it is 0.126 to 0.294. Each interval is on the risk-difference scale and should be interpreted on that scale. These are recalculated intervals, not the intervals from the sponsor’s logistic-regression model.

The sponsor’s reported intervals are for odds ratios: 1.19 to 2.21 for GSK3196165 90 mg versus placebo, 1.02 to 1.89 for 150 mg versus placebo, and 1.62 to 3.37 for tofacitinib versus placebo. Because these are odds-ratio intervals, the reference value for no difference is one. The intervals differ in both scale and method from the simple risk-difference intervals, so they should not be compared as though they were the same estimate.

Intervals describe statistical uncertainty under the analysis used; narrower intervals generally indicate greater precision, while wider intervals indicate less. Precision is not the same as clinical importance, and an interval does not resolve the impact of multiple comparisons or unreported modeling choices. The registry-reported sponsor intervals are identified as .95 intervals, while the secondary non-inferiority analyses report .975 intervals. The full details needed to assess the prespecified interval construction and all associated decision rules are not reported in the registry record.

The recalculated intervals are based on summary counts and an unadjusted method. As the record flags a discrepancy, the sponsor’s own analysis takes precedence for interpreting the trial’s primary analysis. The recalculated intervals are useful as transparent descriptive checks, but their precision should not be mistaken for a complete account of the trial’s analytic uncertainty.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on observed effects, not the trial’s original design calculations. For these binary and continuous outcomes, the listed figures are participants per arm, not total participants. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; each illustration uses the stated fraction of the observed effect as the effect to detect. The original trial’s own sample-size assumptions are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for a hypothetical study to have an 80% chance of detecting the selected effect under those assumptions, if that effect and the assumptions were correct. The 90% power column gives the corresponding planning number for a 90% chance. These are design targets, not guarantees about a future study. The planning table and curve show how those illustrative requirements change when the target effect is altered.

Rows describing a smaller fraction of the observed effect require more participants than rows using the full observed effect. This is a general feature of study planning: smaller differences are harder to distinguish from random variation, so more information is needed. The figures are anchored to effects observed in this trial, which may not be the effects expected in a future study. They should therefore be used to understand the relationship between target effect and planned enrollment, not as a direct recommendation for a new trial.

This is not observed power. It is a planning illustration, not a retrospective measure of whether the trial was adequately powered or a way to reinterpret the observed p-values.

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 = 0.426; treatment proportion p₁ = 0.548; average p̄ = 0.487.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7069 = 1.3854.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7016 = 0.5905.
4. n = (1.3854 + 0.5905)² / (0.1220)² = 262.4, rounded up to 263 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 <- 0.42578125                          # control proportion
p1 <- 0.54775828460039                          # 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(3980483)
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 = 263 (80% power), 351 (90% power)
 75% of observed effect: n per arm = 467 (80% power), 624 (90% power)
 50% of observed effect: n per arm = 1,046 (80% power), 1,400 (90% power)
power.prop.test: 262.4 
Simulated power at n = 263 per arm: 0.802 (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’s sponsor analyses use logistic regression for the Week 12 superiority comparisons and report odds ratios with intervals and p-values. The posted results give odds ratios of 1.62 for GSK3196165 90 mg versus pooled placebo, 1.39 for 150 mg versus pooled placebo, and 2.34 for tofacitinib versus pooled placebo. The corresponding reported p-values are 0.002, 0.036, and < 0.001.

The recalculated values are simple, unadjusted risk differences derived from the posted event counts and denominators. They use a different effect scale and a different calculation from the sponsor’s model. The record flags a discrepancy between the posted summaries and the recalculated comparisons. In that circumstance, the sponsor’s own analysis takes precedence for interpreting the trial’s primary analysis; the recalculations are descriptive checks, not corrections to the sponsor’s result.

The distinction matters because adjusted model estimates may reflect the sponsor’s analysis choices, while an unadjusted recalculation does not reproduce those choices. The available registry information does not give the full model specification needed to recreate the reported results. The results should therefore be read with the sponsor analysis as the inferential analysis and the recalculated contrasts as a separate, transparent view of the posted summary data.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint involves comparisons of multiple active treatment groups with pooled placebo, and the study also reports many secondary outcomes and analyses. Testing several hypotheses increases the chance that at least one result appears statistically notable even when no corresponding effect exists. Statistical procedures for multiplicity can address this issue by controlling the interpretation of a family of tests, but the registry record does not report the full prespecified multiplicity strategy or identify how every result was handled.

The primary endpoint is described as a superiority comparison with placebo, and the sponsor’s analyses are labeled superiority. That information does not establish whether or how multiplicity was controlled across the primary comparisons. The p-values from the recalculations are explicitly unadjusted and should not be treated as multiplicity-adjusted evidence. The registry does not report the full hierarchy of hypotheses, any gatekeeping sequence, or the rules for interpreting secondary outcomes after primary testing.

The primary analysis population is described as the intent-to-treat set of randomized participants who received at least one dose, analyzed according to assigned treatment. This is the population definition stated in the registry, but the phrase does not tell readers how every post-randomization event or missing observation was handled. The registry says multiple imputation was used to handle missing data. The description is truncated, and details such as the imputation model, assumptions about missingness, and sensitivity analyses are not reported in the registry record.

These omissions limit independent assessment of the robustness of the estimates. Missingness can matter when the probability of an unobserved outcome is related to treatment or response, and imputation depends on assumptions about the data-generating process. Without the full analysis plan and missing-data details, the posted results can be described, but the sensitivity of the conclusions to analytic decisions cannot be fully evaluated. No interim-analysis plan or sample-size justification is reported in the registry record.

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: rheumatoid arthritis (2.5%), covid-19 pneumonia (2.0%), neutropenia (1.5%), myocardial infarction (1.5%), vertigo (1.5%).

The registry lists serious adverse events and other adverse events by treatment group, with the number at risk and the number affected. For example, the serious-event counts are 33 among 513 at risk for GSK3196165 90 mg with methotrexate, 39 among 510 for GSK3196165 150 mg with methotrexate, and 23 among 273 for tofacitinib with methotrexate. Pooled placebo lists 8 among 241 at risk. Placebo-switch groups are reported separately. The record also lists deaths by group, including 2, 7, 3, and 1 in the first four listed groups, respectively.

These figures are counts over the reported study groups, not adjusted comparisons of risk. Group sizes and exposure time differ, and the registry record does not provide enough detail to calculate or interpret time-adjusted rates. Serious adverse events are also not equivalent to all adverse events. The list of frequently reported serious-event terms includes rheumatoid arthritis, COVID-19 pneumonia, neutropenia, myocardial infarction, vertigo, and humerus fracture; the listed percentages should be understood as registry-reported terms, not as a complete safety profile.

Raw safety counts do not establish that one treatment is safer than another. They require clinical context, exposure duration, event definitions, and comparative analyses. These registry figures describe reported events and should be read alongside the full safety reporting, which is not reported in the registry record.

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

The primary result describes the proportion meeting a defined ACR20 response threshold at Week 12 in each randomized group. The posted arm percentages and the sponsor’s logistic-regression comparisons provide evidence about that specific endpoint and time point. The simple recalculated risk differences offer an unadjusted absolute comparison, while the sponsor’s odds ratios come from the reported regression analyses. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence.

The result does not establish the size of improvement for every participant, explain which ACR20 component drove the response, or summarize the range of individual experiences. ACR20 is a threshold-based composite: participants just meeting the criterion and those with larger changes both count as responders. Nor does the Week 12 endpoint show whether a response persists through Week 52. Later outcomes are reported separately, including outcomes for participants switched from placebo to active treatment, and should not be conflated with the original placebo comparison.

The result also does not establish an overall benefit-harm balance. Safety counts are reported separately, and the registry record does not supply a complete comparative safety analysis in the information described. Statistical evidence of a difference is not equivalent to clinical importance, and a p-value does not indicate the probability that a treatment effect is true. The clinical importance of the observed contrasts depends on context beyond the endpoint statistics.

Finally, the posted outcome is limited to the trial population: adults with moderately to severely active rheumatoid arthritis who had an inadequate response to methotrexate and met the trial’s participation criteria. The record does not support extrapolation to populations or treatment settings not described. It also does not provide enough detail to independently verify every modeling, missing-data, or multiplicity decision. The findings should therefore be read as trial-specific evidence on a defined response measure, with uncertainty and analytic limits kept in view.

18. Why This Trial Matters Statistically

This trial illustrates why the effect scale matters. A percentage meeting a response threshold, an absolute risk difference, and a logistic-regression odds ratio all describe the same general comparison from different perspectives, but they are not numerically interchangeable. Readers need to know which scale is being used before assessing the size and precision of a reported contrast.

It also shows the distinction between registry summaries and the sponsor’s inferential analysis. Posted counts allow transparent, unadjusted recalculations, but those calculations cannot reproduce an incompletely described regression model. When the record flags a discrepancy, the sponsor’s own analysis takes precedence rather than treating the simpler calculation as a substitute.

The trial’s many endpoints and comparisons make multiplicity an important interpretive issue. A primary outcome can be clearly identified while the interpretation of a broader family of secondary tests remains uncertain if the adjustment strategy is not reported. This is a reason to give primary and secondary results different weight, rather than treating every nominal p-value as equally confirmatory.

Finally, the sample-size illustrations demonstrate how planning depends on the target effect and assumptions. They are not the original design rationale and do not measure observed power. Separating these planning calculations from the trial’s actual analysis helps avoid overstating what can be learned from registry-level results.

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 leaves important statistical details unavailable. The full statistical analysis plan, original sample-size justification, and complete primary model specification are not reported. The missing-data description is truncated after stating that multiple imputation was used, so the imputation model, assumptions, and sensitivity analyses cannot be assessed. Multiplicity handling across the primary and secondary comparisons is also not reported in enough detail to determine how family-wise interpretation was controlled.

The placebo groups were pooled for analyses through Week 12, and separate placebo-switch groups are listed for later treatment. The Week 12 comparison therefore has a pooled placebo reference, while later outcomes may involve different treatment histories. Results across these periods should not be treated as a single unchanged randomized comparison.

The registry flags a discrepancy between the sponsor’s results and simple recalculations from posted summary statistics. The recalculations are unadjusted and cannot replicate the sponsor’s logistic-regression estimates without the full model specification. They should be read as descriptive checks only. The registry also reports later non-inferiority analyses without reporting the margin or complete decision framework, limiting independent evaluation of those claims.

Safety counts are presented by group, but the listed figures do not provide an adjusted comparison or a full account of exposure time. Registry adverse-event summaries are not a substitute for a detailed safety analysis. These limitations constrain how far the posted results can support broader conclusions about robustness, treatment comparisons across all time points, or overall safety.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of GSK3196165 Versus Placebo and Tofacitinib in Participants With Moderately to Severely Active Rheumatoid Arthritis Who Have an Inadequate Response to Methotrexate — NCT03980483.
• Registry record last updated 2024-03-27; status last verified 2024-03.
• Results first posted 2023-10-25.
• 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

NCT03980483 is a completed, randomized, double-blind, parallel-group phase 3 study of GSK3196165 with methotrexate in participants with moderately to severely active rheumatoid arthritis and an inadequate response to methotrexate. It also included tofacitinib with methotrexate and placebo groups that switched to active treatment after Week 12.

The primary endpoint was ACR20 response at Week 12, with superiority comparisons against pooled placebo. The registry reports arm percentages, sponsor logistic-regression odds ratios, secondary outcomes, and adverse-event counts. The primary analysis population is described as randomized participants who received at least one dose, analyzed by randomized group, with multiple imputation noted for missing data.

The record does not report the full statistical plan, original sample-size justification, multiplicity strategy, or enough missing-data and model detail for complete independent reconstruction. A discrepancy is flagged between sponsor results and simple unadjusted recalculations, so the sponsor’s own analysis takes precedence.