Safety and Efficacy of Pf-06650833 In Subjects With Rheumatoid Arthritis, With An Inadequate Response To Methotrexate: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of Pf-06650833 In Subjects With Rheumatoid Arthritis, With An Inadequate Response To Methotrexate (NCT02996500), a randomized phase 2 study. The primary outcome is Change From Baseline in the Simplified Disease Activity Index (SDAI) at Week 12.

2. Clinical Question

3. Trial Design

This was a Phase 2, randomized, double-blind, double-dummy, parallel-group, multicenter study of PF-06650833 in rheumatoid arthritis. The registry records enrollment of 269 participants and a completed trial. The study started on 2016-11-10, and primary completion was recorded as 2018-08-15.

Participants were assigned to placebo, tofacitinib, or one of four once-daily PF-06650833 dose groups: 20 mg, 60 mg, 200 mg, and 400 mg. Treatment continued for 12 weeks. The brief summary says PF-06650833 or matching placebo tablets were taken orally once daily under fasting conditions, while tofacitinib or matching placebo tablets were taken orally twice daily. The double-dummy design used matching tablets to support blinding across regimens with different schedules. The registry labels masking as triple, though it does not explain which roles were masked.

The primary comparison structure focused on each PF-06650833 dose against placebo. Tofacitinib was an active comparator, but its efficacy endpoint was exploratory and was not designated as a primary or secondary endpoint. Thus, the active-control arm should not be treated as an additional confirmatory comparison for the primary question.

The listed primary outcome was change from baseline in SDAI at Week 12. Secondary outcomes included additional SDAI assessments and disease-activity thresholds based on SDAI and DAS28 measures at several follow-up times. A fatigue measure was also posted. The registry record does not report the planned sample-size justification, details of interim analyses, or a full multiplicity strategy. The recorded enrollment is therefore a description of trial conduct, not by itself an explanation of how the study’s planned precision or power was chosen.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis population included all participants who were randomized to the study, received at least 1 dose of the randomized investigational drug (PF-06650833, or placebo), and had data collected for this outcome measure at the time points assessed. It was pre-specified in the protocol to not summarize this efficacy endpoint for Tofa arm.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: The Intent-to-Treat (ITT) population was defined as all participants who were randomized to study treatment and received at least 1 dose of the randomized investigational drug (PF-06650833, tofacitinib, or placebo).

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in the Simplified Disease Activity Index (SDAI) at Week 12, measured over Baseline and Week 12.

The primary endpoint was change from baseline in the Simplified Disease Activity Index at Week 12. SDAI is a continuous composite measure built from tender or painful joint count and swollen joint count using 28 joints, patient and physician global assessments, and high-sensitivity C-reactive protein. The registry describes a total score ranging from 0 to 86, with lower activity categories at lower scores. The outcome therefore combines clinical assessments with an inflammatory marker rather than relying on a single symptom or laboratory value.

Change from baseline expresses how much the score shifted over the treatment period. A negative change indicates a decrease in SDAI; a more negative mean change reflects a larger average decrease in the observed group. The endpoint is useful for comparing changes across treatment groups while preserving information across the scale, rather than reducing every participant’s score to a category such as remission or low disease activity.

The score’s components have different units and meanings, but the registry’s formula combines them into a single index. This can make a continuous measure more sensitive to variation in disease activity than a threshold outcome, while making the result less immediately interpretable as a change in one particular symptom. The endpoint does not, by itself, describe every aspect of benefit or harm, and the Week 12 result does not establish longer-term effects.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

Several statistical ideas help distinguish what the trial’s summaries say from what they do not say. The explanations below are general statistical guidance, followed by how those ideas apply to the registry’s reported analyses.

What does a change score represent?

In general, a change score subtracts a participant’s baseline measurement from a later measurement. The group mean change summarizes the average shift among the participants included in that analysis. It is not the same as the treatment effect, because participants in the control group may also change over time. In a randomized trial, the treatment contrast is commonly expressed by comparing the groups, with any adjustment specified by the analysis model.

Here, all listed arm-level SDAI changes are negative. That establishes that average scores decreased in the analyzed groups, but the placebo group also had a negative mean change. The sponsor’s ANCOVA comparisons are the relevant reported estimates for the dose-versus-placebo question. They should not be replaced by subtracting the posted arm means: that would be a simple, unadjusted calculation and would not reproduce the model-based analysis.

What does ANCOVA contribute?

In general, analysis of covariance (ANCOVA) compares outcome values across groups while adjusting for one or more covariates, often including baseline outcome. Adjustment can account for chance differences in baseline values and may improve precision when the covariates predict the outcome. The interpretation depends on the model, included covariates, population, and handling of missing measurements. The registry identifies ANCOVA for the reported primary comparisons, but the full covariate specification and all model diagnostics are not reported in the registry record.

The primary outcome description adds an important qualification: the primary analysis used Bayesian ANCOVA with an informative placebo prior that borrowed from historical tofacitinib placebo data. In general, a Bayesian prior represents information incorporated into the analysis before considering the current trial data. Borrowing historical control information can influence the estimate and uncertainty, depending on the prior and model. The exact prior specification and sensitivity analyses are not reported in the registry record, so the degree and robustness of borrowing cannot be assessed from the registry description alone.

How should interval estimates be read?

In general, an interval estimate communicates uncertainty around an estimated effect. A confidence interval is constructed by a procedure that, under its assumptions and repeated use, has a specified coverage property. A Bayesian credible interval instead summarizes posterior uncertainty under the model and prior. The two are not interchangeable labels even when both are written with lower and upper endpoints.

The primary endpoint description calls its interval a credible interval, while the listed comparison results label their intervals as 95% confidence intervals. The record does not resolve that difference in terminology. The interval endpoints for the reported comparisons are all negative, which is consistent with a greater decrease relative to placebo under those analyses. Interval width also matters: it communicates uncertainty, and estimates should not be judged only by whether an interval crosses zero. The reported p-values offer another summary of evidence under the specified tests, not the probability that a treatment effect is true.

Why distinguish arm estimates from contrasts?

In general, an arm estimate describes a group, whereas a contrast directly compares groups. Arm-level intervals may overlap even when a model-based contrast is estimated with an interval that excludes zero, or the reverse; overlap of separate arm intervals is not itself a formal test of the difference. The model can account for baseline and other design features in ways that simple visual comparison cannot.

The registry reports one arm-level SDAI change and interval for each placebo and PF-06650833 group, plus dose-versus-placebo ANCOVA results. Those are complementary summaries. The 200 mg comparison is identified as a median difference, unlike the mean differences reported for the other doses. That makes it especially important not to present all four estimates as if they were the same estimand.

What can the secondary planning illustrations show?

In general, a sample-size calculation asks how many participants would be needed under stated assumptions to detect a specified effect with a target probability of statistical significance. The registry’s planning illustrations use the observed effect for the FACIT-F comparisons and also consider smaller fractions of that effect. They assume a two-sided significance level of 0.05, equal allocation, and a normal approximation. These are planning illustrations, not the trial’s own design justification and not observed power.

Observed power is not a useful substitute for an uncertainty interval after results are known: it largely restates the observed effect and its standard error. The illustrated participant counts depend on the assumed effect, allocation, outcome variability, and approximation. They do not show what the trial was actually designed to detect, because the planned sample-size justification is not reported in the registry record. They also concern the FACIT-F comparisons, not the primary SDAI analysis.

The FACIT-F re-calculations are unadjusted comparisons derived from posted summary statistics. In general, such re-calculations can help readers understand the scale of a difference and its uncertainty, but they do not reproduce an analysis that adjusts for baseline or other covariates. Their p-values are unadjusted and should not be treated as confirmatory evidence across a set of many outcomes and comparisons.

Why does multiplicity matter?

In general, testing several doses, outcomes, and follow-up times creates multiple opportunities for a nominally small p-value to occur by chance. A prespecified multiplicity procedure can control the overall false-positive risk or organize which tests are confirmatory. The registry record does not report a full multiplicity adjustment or testing hierarchy. Consequently, the listed p-values should be read as reported comparisons, not as evidence that a family-wide error rate was controlled.

10. Analyses Reported by the Sponsor

The primary results in the registry are sponsor-reported ANCOVA comparisons of each PF-06650833 dose against placebo. They are not simple calculations from the group means. The primary outcome description states that the primary analysis used Bayesian ANCOVA with an informative placebo prior borrowing from historical tofacitinib placebo data, while the comparison listings use the label ANCOVA and report 95% intervals and p-values. The record does not give enough detail to reconstruct the model or resolve every difference in terminology.

The sponsor-reported treatment contrasts are the appropriate results to cite for the trial’s primary analysis. The separate recalculations described in the registry concern FACIT-F, a secondary continuous outcome, and are unadjusted calculations from posted summary statistics. They are not a recalculation of the primary SDAI analysis and do not validate or replace the Bayesian ANCOVA results. The registry does not flag a discrepancy between its primary result and a recalculation.

The 200 mg primary contrast is labeled a median difference, whereas the other dose contrasts are labeled mean differences. That distinction should be retained when describing the reported results. Because the model specification, prior details, and analysis diagnostics are not reported in the registry record, independent reproduction of the sponsor’s primary model-based results is not possible from the reported summaries alone. The sponsor’s own analysis remains the source for the primary inferential results; simple arithmetic on the arm summaries should not be presented as an alternative adjusted estimate.

11. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when an analysis considers several doses, endpoints, time points, or pairwise comparisons. Even if each test uses the same nominal threshold, the chance of at least one apparently positive result can increase across a family of tests. In general, trial protocols can address this with a prespecified hierarchy, adjusted significance thresholds, or another defined procedure. The registry record does not report a complete multiplicity strategy for the primary dose comparisons or the broad secondary outcome program. The reported p-values should therefore be understood as the values attached to the listed comparisons, not assumed to control a family-wise error rate.

Missing data can also affect interpretation. The stated primary analysis population required randomization, at least one dose of study drug, and outcome data at the assessed time points. This is not an all-randomized population definition: participants lacking a required dose or outcome measurement may not be included in that analysis population. The registry text truncates its description of the prespecified population, and the detailed rules for missing measurements, discontinuation, and sensitivity analyses are not reported in the registry record.

In general, complete-case or observed-data analyses can be biased if the probability of having an outcome recorded is related to treatment or outcome status. Model-based methods can address some missingness patterns under assumptions, but those assumptions need to be described and examined. The registry summary does not provide enough information to determine precisely how missing Week 12 data were handled or how sensitive the estimates are to alternative assumptions.

The primary analysis used an informative placebo prior that borrowed from historical tofacitinib placebo data. Bayesian borrowing is a modeling choice, not a substitute for transparent missing-data and multiplicity procedures. The exact prior, robustness checks, and relationship between the primary estimand and the reported comparison tests are not reported in the registry record. The absence of those details does not establish that the analyses were inappropriate; it limits what can be independently evaluated from the registry entry.

The registry also does not report the planned sample-size justification or interim-analysis details. Enrollment alone cannot establish the intended detectable effect or whether the study was sized for a particular confirmatory objective. The secondary sample-size illustrations use observed FACIT-F effects and stated planning assumptions; they should not be mistaken for the original design plan.

12. 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: hepatotoxicity (2.6%), epididymitis (2.6%), pneumonia bacterial (2.3%), acute myocardial infarction (2.1%), appendicitis (2.1%).

The posted safety figures count participants with serious adverse events and participants with other adverse events within each listed safety group. Serious events were reported for 1 participant in placebo, 1 in the Tofa 10 mg group, 1 in PF-06650833 20 mg, 1 in 60 mg, 1 in 200 mg, and 3 in 400 mg. The registry reports 0 deaths in each listed group. Other adverse events were reported for 10, 8, 12, 11, 9, and 11 participants, respectively, across those same listed groups.

These are counts, not comparative risk estimates. The groups have different numbers at risk, and the figures do not describe event timing, duration, recurrence, severity beyond the serious-event classification, or exposure-adjusted rates. The registry lists several serious-event terms with percentages, including hepatotoxicity and epididymitis at 2.6%, bacterial pneumonia at 2.3%, and acute myocardial infarction, appendicitis, and subdural haematoma at 2.1%. Those listings do not establish causation or permit a reliable comparison of risks across treatment groups.

The safety label “Tofa 10 mg” differs from the arm description of tofacitinib 5 mg twice daily, and the registry record does not reconcile the labels. Sparse event counts and a 12-week study period limit interpretation of uncommon or delayed events. These data describe what was reported during the trial; they do not establish that a regimen is safe or unsafe.

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

The primary result is a comparison of Week 12 SDAI change in a selected analysis population of a randomized trial among people with active rheumatoid arthritis and an inadequate response to methotrexate. The reported dose-versus-placebo contrasts are negative, with the listed 95% intervals below zero. In the context of a scale where lower values indicate less disease activity, this is evidence of a larger decrease in SDAI for the PF-06650833 groups under the reported analyses.

The result does not mean that every participant improved, or that the observed group averages describe each individual’s experience. It does not establish a specific benefit for every outcome, and the fatigue endpoint is distinct from SDAI. The primary endpoint is a composite score; a change in that score does not identify which component drove the group-level result.

The result is limited to the trial’s 12-week treatment period and to the analysis population described in the registry. It does not establish what happens over longer follow-up, in people with other disease histories, or under treatment conditions not described in this trial. The record also does not report enough detail to independently assess all missing-data assumptions, the full ANCOVA specification, prior sensitivity, or multiplicity control.

The reported interval estimates communicate uncertainty rather than certainty. The primary analysis description identifies Bayesian ANCOVA and an informative placebo prior, while the listed comparisons report ANCOVA estimates, 95% intervals, and p-values. Those elements should be interpreted in light of the registry’s limited methodological detail. The 200 mg contrast is reported as a median difference, while the other contrasts are reported as mean differences, so they are not all precisely the same summary measure.

Finally, a statistically distinguishable group contrast is not the same as a conclusion about clinical importance. The registry record does not supply a threshold for a clinically meaningful between-group difference in SDAI. The posted results describe an estimated difference under the trial’s model, not a universal treatment ranking or a recommendation for an individual.

14. Why This Trial Matters Statistically

This trial illustrates why arm-level change and treatment contrast must be kept separate. Each reported group had a decrease in SDAI, including placebo. The dose-versus-placebo estimates address the randomized comparison more directly than the arm means alone, while the ANCOVA model and Bayesian prior affect how those contrasts are estimated and how uncertainty is represented.

It also highlights the importance of identifying the estimand. The registry’s dose comparisons are mostly reported as mean differences, but the 200 mg comparison is labeled a median difference. That distinction affects what summary of the outcome is being compared. A reader should not casually place all estimates on the same footing without noting the differing labels.

The primary analysis description combines Bayesian modeling with historical placebo borrowing. This makes the analysis more than a conventional comparison of observed group averages. Understanding the prior and its sensitivity matters because historical information can influence the estimate and its uncertainty. The registry’s description is informative about the broad approach but does not provide enough detail for a full independent audit.

The study also shows why secondary results need a different evidential weight. The registry reports a diverse set of secondary measures and time points, while the numerical FACIT-F comparisons are unadjusted re-calculations. Without a reported multiplicity plan, isolated secondary p-values should not be treated as if they were independent confirmatory tests. Planning illustrations based on observed secondary effects can inform future study design but are not observed power and do not reveal the trial’s original design assumptions.

Finally, the record separates efficacy and safety questions but gives limited safety detail for interpreting comparative risk. Counts of adverse events provide a useful description, yet sparse events, unequal group sizes, and short follow-up constrain causal or long-term conclusions. Taken together, the statistical value of the trial lies not just in its estimates, but in understanding the assumptions and limits attached to them.

15. 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.

Several features of this specific record limit independent interpretation. The primary endpoint description says the analysis used Bayesian ANCOVA with an informative placebo prior based on historical tofacitinib placebo data, but it does not report the prior specification, degree of borrowing, or sensitivity analyses. The comparison listings are labeled ANCOVA and give p-values and 95% intervals, while the endpoint description calls the interval a credible interval. The registry does not explain this difference in reporting terminology.

The 200 mg contrast is reported as a median difference, whereas the other dose contrasts are reported as mean differences. This makes the set of dose estimates less directly comparable than a uniform estimand would be. The full model covariates and diagnostics are not reported in the registry record, so the model-based estimates cannot be reconstructed from the posted arm summaries.

The primary analysis population required treatment exposure and outcome data at assessed time points. The registry text describing that population is truncated, and detailed missing-data rules and sensitivity analyses are not reported in the registry record. The record also does not report the complete multiplicity plan, sample-size justification, or interim-analysis details. These omissions prevent assessment of how the study was planned for precision and how the nominal tests were organized across doses and outcomes.

The primary follow-up was Week 12, which limits conclusions about durability. The active-control efficacy endpoint was exploratory, so the record does not support treating the trial as a primary head-to-head comparison against tofacitinib. The safety results include a mismatch between the tofacitinib dose description and the safety group label, which is not reconciled. Finally, detailed numerical results for all listed secondary outcomes are not reported in the registry record, restricting a full assessment of consistency across those outcomes.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Safety and Efficacy of Pf-06650833 In Subjects With Rheumatoid Arthritis, With An Inadequate Response To Methotrexate — NCT02996500.
• Registry record last updated 2020-02-27; status last verified 2020-02.
• Results first posted 2020-02-27.
• 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.

19. Record Summary

The registry describes a completed Phase 2, randomized, double-blind, double-dummy, parallel-group study in active rheumatoid arthritis with inadequate response to methotrexate. Enrollment was 269, and treatment lasted 12 weeks. Four once-daily PF-06650833 doses were compared with placebo; tofacitinib was included as an active comparator, with its efficacy endpoint designated exploratory.

The primary outcome was change from baseline in SDAI at Week 12. The listed sponsor analyses report dose-versus-placebo ANCOVA contrasts, with estimates below zero and reported intervals below zero. The endpoint description identifies a Bayesian ANCOVA with an informative placebo prior, while the registry does not provide all details needed to reconstruct or fully evaluate that model.

Secondary outcomes include additional disease-activity measures and FACIT-F. The posted FACIT-F recalculations are unadjusted and do not replace the sponsor’s primary analysis. Multiplicity procedures, detailed missing-data methods, and the original sample-size justification are not reported in the registry record. Safety counts are descriptive and should not be interpreted as proof of comparative safety.