SMART Study: A Study of Re-treatment With MabThera (Rituximab) in Patients With Rheumatoid Arthritis Who Have Failed on Anti-TNF Alfa Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for SMART Study: A Study of Re-treatment With MabThera (Rituximab) in Patients With Rheumatoid Arthritis Who Have Failed on Anti-TNF Alfa Therapy (NCT01126541), a randomized phase 3 study. The primary outcome is Disease Activity Score Based on 28-Joints Count and C-Reactive Protein (DAS28-CRP) Area Under the Curve (AUC) at Week 104.

2. Clinical Question

The question is about the relative course of a disease-activity measure following different retreatment regimens, not about whether rituximab is better than no treatment. Both randomized groups received rituximab initially, and the later comparison was between one and two additional infusions. The primary endpoint is a continuous summary over time, so it reflects both the level and duration of measured disease activity rather than a single visit alone.

3. Trial Design

This was a completed Phase 3, randomized, parallel-group study with no masking. The registry lists enrollment of 224 and a study period beginning in 2006-09, with primary completion in 2011-11. Hoffmann-La Roche is listed as sponsor. The study enrolled people with rheumatoid arthritis who had active disease and an inadequate response or intolerance to anti-TNF therapy.

All participants were to receive 1000 mg intravenous rituximab on Days 1 and 15. At Week 24, participants who demonstrated a moderate or good response were randomized to receive either one or two additional 1000 mg infusions. The randomized comparison therefore concerns a selected group who met the response condition at Week 24, rather than everyone enrolled at the beginning of the study. The registry record does not report how many participants met that condition or the exact timing of each retreatment infusion.

The primary endpoint was assessed at Week 104 in the per-protocol population. That population is defined as randomized participants in the intent-to-treat population without major protocol violations, analyzed according to their initially assigned arm regardless of treatment received. The primary arm summaries include 51 participants in Arm A and 49 in Arm B. The registry also reports a secondary AUC weighted-time analysis with 70 and 73 participants, respectively; the reasons for the differing analysis populations are not reported in the registry record.

The study was unmasked, and the registry record does not describe allocation concealment or the procedure used to generate the randomization sequence. It also does not report the original sample-size justification, planned interim analyses, or the full statistical analysis plan. These omissions limit how fully the design and analysis decisions can be reconstructed from 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per Protocol (PP) population: all randomized participants in the Intent-to-Treat (ITT) population (defined as all randomized participants) without major protocol violations. Participants were grouped according to their initially assigned treatment arm irrespective of the treatment actually received.

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 Disease Activity Score Based on 28-Joints Count and C-Reactive Protein (DAS28-CRP) Area Under the Curve (AUC) at Week 104, measured over Week 104.

The primary endpoint is the area under the curve for DAS28-CRP from Day 1 through Week 104. DAS28-CRP is based on swollen and tender joint counts, the participant’s overall assessment, and serum C-reactive protein levels. The score ranges from 0 to 9.4, with higher scores indicating more disease activity. A score at or below 3.2 implies low disease activity, a score greater than 3.2 to 5.1 implies moderate to high disease activity, and a score below 2.6 corresponds to remission.

An AUC combines repeated measurements across time. Here, the registry describes use of a trapezoidal method with actual visit dates to account for the time between assessments. The resulting score-on-a-scale-times-week quantity represents the accumulated measured disease activity, rather than the score at a single visit. A larger AUC generally corresponds to more disease activity accumulated over the period, while a lower AUC corresponds to less.

Using an AUC can be useful when a treatment comparison concerns the overall pattern of repeated disease-activity measurements. It incorporates both the measured values and the time separating them. The endpoint is nevertheless dependent on which visits were observed and on how missing or late measurements were handled. The registry describes censoring at Week 104 and linear extrapolation using the Weeks 96 and 104 values to obtain a value at the true Week 104, but fuller missing-data procedures are not reported in the registry record.

7. Results Posted in the Registry

• Randomized Retreatment Arm B: Rituximab 1000 mg x 2: mean 2,666 versus 2,761 on control; difference -95.40 (95% CI -1,479 to 1,288), standardized effect d = -0.03; z-test p = 0.893.

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.

DAS28-CRP AUC Weighted Time

• 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 deviations.
• Result:
  • Randomized Retreatment Arm B: Rituximab 1000 mg x 2: mean 3.88 versus 3.82 on control; difference 0.06 (95% CI -0.17 to 0.29), standardized effect d = 0.08; z-test p = 0.613.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Randomized Retreatment Arm B: Rituximab 1000 mg x 2 and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 39 secondary outcome measures. They cover repeated DAS28-CRP measurements, changes from baseline, remission and low disease activity thresholds, weighted time, and time to reach disease-activity categories after initial treatment or retreatment. This set of outcomes addresses different aspects of the disease-activity course: average level, threshold attainment, and timing of a response. A complete numerical account of all 39 secondary measures is not available in the registry record.

The posted weighted-time AUC comparison is broadly consistent with a small observed difference and uncertainty spanning zero, but it is not the same endpoint or analysis population as the primary per-protocol AUC. It can provide context about the course of disease activity, but it cannot settle the primary comparison or establish equivalence. Other secondary outcomes may be informative about particular response definitions or time points, but their estimates and uncertainty are not reported in the registry record.

Secondary findings generally carry less evidential weight when many outcomes are examined without a clearly reported multiplicity strategy. Testing multiple outcomes increases the opportunity for apparently notable results to arise by chance. The registry record does not report whether multiplicity adjustments were planned or applied, nor does it provide a complete statistical analysis plan. Accordingly, isolated secondary findings should be treated as exploratory unless their prespecification and inferential handling are documented.

The secondary outcomes are useful for understanding how the investigators framed disease activity beyond the primary AUC. They do not replace the primary endpoint, and their interpretation depends on their own populations, definitions, timing, and missing-data handling. The registry does not report enough detail to determine whether the secondary analyses were confirmatory, supportive, or exploratory.

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

• DAS28-CRP During the Initial Treatment
• DAS28-CRP and Changes From Baseline to Week 24 in DAS28-CRP by Retreatment Course
• Percentage of Participants Achieving Clinical Remission (DAS28-CRP <2.6) or Low Disease Activity (DAS28-CRP ≤3.2)
• DAS28-CRP AUC Weighted Time
• Time to Achieve DAS28-CRP Remission After the First Course
• Time to Achieve DAS28-CRP Remission After Retreatment
• Time to Achieve DAS28-CRP ≤3.2 After the First Course of Treatment
• Time to Achieve DAS28-CRP ≤3.2 After Retreatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numeric AUC rather than a binary event or a time-to-event measure. The reported arm summaries are means with standard errors. A mean gives the arithmetic average of the observed endpoint values in a group. A standard error describes the precision of that estimated mean; it is not the same quantity as the spread of individual participant values. The primary arm summaries are reported for the per-protocol population.

What does the AUC calculation represent?

The registry describes DAS28-CRP measurements at protocol visits from Day 1 through Week 104 and an AUC calculated using the trapezoidal method. Conceptually, the method connects adjacent measurements with straight-line segments and estimates the area under those segments. Visit dates, rather than only nominal visit labels, were used to represent elapsed time. This is intended to account for variation in the time between actual assessments. The resulting AUC has units of score on a scale multiplied by week.

Because disease activity is measured repeatedly, an AUC summarizes the course across the observation period. It is not simply the average of the endpoint scores at one visit, and it does not reveal every change in the trajectory. Distinct patterns of scores can produce similar AUC values. The endpoint also depends on how measurements between visits are represented and on the treatment of measurements that are absent or occur outside the target visit window.

How should the mean difference be read?

The unadjusted recalculation compares the two group means by subtracting the Arm A mean from the Arm B mean. A negative estimate means the observed mean AUC was lower in Arm B; a positive estimate would mean it was higher. The estimate is a summary of the observed group averages, not an adjusted causal effect. The recalculated confidence interval and p-value use the posted summary statistics and are explicitly unadjusted. They do not account for any covariates or other features that may have been used in the sponsor’s analysis.

The standardized effect estimate, d, expresses the mean difference in relation to the pooled standard deviation. It can help describe the difference on a common scale, but it does not replace the difference in the endpoint’s original units. A standardized effect also depends on the variability in the population. The posted primary comparison reports d as -0.027. It should be interpreted as a small standardized point estimate alongside the wide uncertainty in the original-unit difference, not as proof of equivalence.

Why do the two analyses differ?

The registry reports an adjusted difference of 51.38 and a 95% confidence interval from -131.22 to 233.98, while the unadjusted recalculation gives a different point estimate and interval. Adjusted and unadjusted analyses can differ because their estimands and statistical procedures differ. The registry does not state the method for the reported adjusted analysis, nor does it provide the covariates or detailed model specification. The exact source of the difference therefore cannot be determined from the registry record. The reported result is also categorized as non-inferiority or equivalence type, but the margin and decision rule are not reported in the registry record.

For the secondary AUC weighted-time measure, the registry reports means and standard deviations, rather than standard errors, for its arm summaries. The mean difference and interval posted for this outcome are also unadjusted recalculations. The distinction between standard deviation and standard error matters: standard deviation describes variation among observed values, whereas standard error describes uncertainty in the estimated mean. The same type of summary should not be assumed across the primary and secondary endpoints.

What do p-values and confidence intervals contribute?

A p-value evaluates how compatible the observed data are with a specified null hypothesis under the assumptions of the analysis. It does not give the probability that the null hypothesis is true, nor does it measure clinical importance. A confidence interval gives a range of effect estimates compatible with the data and the statistical procedure at its stated confidence level. Both are affected by sample size, variability, and analysis choices. For the primary unadjusted comparison, the reported p-value is 0.893 and the 95% interval spans negative and positive differences. That combination indicates limited precision for distinguishing the direction and magnitude of the group difference.

Over-dispersion is a concern when observed variability exceeds what a model’s assumptions allow, which can make standard errors too small and intervals too narrow if not handled appropriately. The registry record does not report a count-model outcome for this primary endpoint or an over-dispersion assessment. For a continuous AUC outcome, the central concerns visible in the posted summaries are the amount of variability, the sample sizes, and the analysis population. Whether the sponsor assessed distributional assumptions or robustness is not reported in the registry record.

11. Confidence Intervals and Precision

The primary unadjusted recalculated mean difference is -95.4, with a 95% confidence interval from -1479.0 to 1288.0. The interval is wide in relation to the point estimate and includes both negative and positive values. Thus, the estimate does not pin down the direction of the underlying mean difference. It is compatible with lower mean AUC in Arm B, little difference, or higher mean AUC in Arm B, within the limits of this unadjusted calculation.

A confidence interval is not a range containing a fixed proportion of individual participants’ results. It describes the uncertainty in an estimated group difference under the statistical method and its assumptions. A wide interval indicates limited precision: estimates substantially different from the point estimate remain compatible with the data. It should not be read as a probability statement about the true effect, and it does not establish whether any particular value is clinically important.

The adjusted analysis has a 95% confidence interval from -131.22 to 233.98 around an adjusted difference of 51.38. This interval also crosses zero. Because the adjusted method and its target estimand are not described in the registry record, the interval cannot be fully assessed against the unadjusted recalculation. The registry’s classification of the result as a non-inferiority or equivalence type does not resolve that limitation: the margin and decision rule are not reported in the registry record.

The secondary weighted-time comparison has a 95% confidence interval from -0.173 to 0.293. It, too, includes zero. Its outcome scale and analysis population differ from the primary endpoint, so its precision should be interpreted in relation to that secondary measure rather than as a direct measure of precision for the primary AUC result.

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 figures are participants per arm for the continuous-outcome comparisons, not total events. They are illustrative calculations based on the observed effect and assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning effect is set at 100%, 75%, or 50% of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm under which a study would have an 80% chance of detecting the specified effect at the stated significance level, if the planning assumptions hold. The 90% power column represents a higher chance of detecting that effect under those assumptions and therefore requires more participants. For example, for planning at 100% of the observed primary effect, the figures are 21,529 participants per arm for 80% power and 28,821 participants per arm for 90% power. Planning for 75% of the observed effect gives 38,273 and 51,236 participants per arm, respectively. Planning for 50% gives 86,113 and 115,281.

Smaller effects require more participants because they are harder to distinguish from random variation. The same principle applies to the secondary weighted-time comparison, for which the illustrative figures are based on its own observed effect and variability. These calculations are not observed power. They are planning illustrations derived from the observed effects, and they should not be treated as evidence that the completed study had a particular probability of detecting an effect.

The figures are unusually large in relation to the primary analysis sample sizes. That reflects the small observed standardized difference used in the planning calculation; it does not show that the trial was designed around those numbers. The registry record’s enrollment of 224 and the endpoint analysis counts describe the study, while the planning calculations are hypothetical scenarios for detecting selected fractions of an observed difference.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -95.400; pooled standard deviation σ = 3532.910.
2. n = 2 × (1.96 + 0.842)² × 3532.910² / -95.400² = 21,528.1, rounded up to 21,529 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
delta <- -95.4000000000001                      # observed difference in means
sigma <- 3532.91043562138                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(1126541)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 21,529 (80% power), 28,821 (90% power)
 75% of observed effect: n per arm = 38,273 (80% power), 51,236 (90% power)
 50% of observed effect: n per arm = 86,113 (80% power), 115,281 (90% power)
power.t.test: 21529.1 
Simulated power at n = 21,529 per arm: 0.800 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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-reported primary analysis gives an adjusted difference of 51.38, with a 95% confidence interval from -131.22 to 233.98. It is classified as a non-inferiority or equivalence type analysis. No p-value, analysis method, non-inferiority or equivalence margin, or decision rule is reported in the registry record. Without those details, the adjusted result cannot be used to determine whether a prespecified non-inferiority or equivalence criterion was met.

The unadjusted recalculation compares the posted arm means directly. It gives a mean difference of -95.4, with a 95% confidence interval from -1479.0 to 1288.0 and an unadjusted p-value of 0.893. This calculation is not the sponsor’s adjusted analysis and should not be treated as if it were. Differences in adjustment, analysis population, or estimand can lead to different estimates; the registry record does not give enough methodological detail to identify the specific reason for the difference.

The two analyses both have intervals that include zero, but that fact does not demonstrate equivalence. The sponsor’s analysis is the registry-reported analysis, while the recalculation is a transparent, unadjusted comparison based on group summaries. Interpretation of the sponsor’s non-inferiority or equivalence claim requires the margin and full analysis specification, which are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists many secondary measures in addition to the primary endpoint. When several outcomes or analyses are tested, the chance of at least one apparently positive result can increase. A multiplicity plan may control that risk through prespecified testing order or statistical adjustment. Whether such a plan was specified or used is not reported in the registry record. The posted unadjusted secondary comparisons therefore should not be interpreted as if they were protected from multiple testing.

The registry describes the primary analysis population as per protocol: randomized intent-to-treat participants without major protocol violations, grouped according to their initially assigned arm irrespective of treatment received. It also defines the intent-to-treat population as all randomized participants. This differs from a strict analysis of everyone randomized if participants with major violations are excluded from the primary per-protocol set. The registry does not report the number excluded for protocol violations or the specific violations.

The primary endpoint counts are 51 in Arm A and 49 in Arm B, whereas the secondary weighted-time analysis counts are 70 and 73. Reasons for the differing counts, including missing measurements, analysis eligibility, or other exclusions, are not reported in the registry record. The record describes censoring at Week 104 and linear extrapolation using the Weeks 96 and 104 values to obtain the value at the true Week 104. It does not report fuller details of missing-data assumptions, sensitivity analyses, or how participants with incomplete visit histories contributed to the endpoint.

The original sample-size justification, interim analyses, randomization procedures, statistical model for the adjusted result, and complete analysis plan are not reported in the registry record. These missing details constrain assessment of prespecification, selection of analysis populations, robustness to missingness, and the basis for the reported non-inferiority or equivalence classification. The registry’s lack of these details is not evidence that the procedures were absent; it means they cannot be evaluated from 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 0% 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 (5.9%), osteoarthritis (3.0%), arthralgia (2.9%), diabetes mellitus inadequate control (2.5%), arthropathy (1.5%).

For serious adverse events, the registry reports 19 affected participants among 66 at risk in randomized Arm A and 25 among 68 at risk in randomized Arm B. The counts describe participants with at least one serious adverse event as presented in the registry; they are not counts of all event episodes. The record also lists a nonrandomized rituximab group with 16 affected among 81 at risk. Because that group was not randomized, it should not be treated as a directly comparable randomized arm.

For other adverse events, the registry reports 61 affected among 66 at risk in Arm A and 65 among 68 at risk in Arm B. These descriptive figures do not, on their own, show whether events were related to treatment or establish a comparative safety effect. Differences in follow-up, event definitions, and participant characteristics can matter, and detailed methods for those matters are not reported in the registry record.

The most frequently listed serious-event terms include rheumatoid arthritis at 5.9%, osteoarthritis at 3.0%, arthralgia at 2.9%, and diabetes mellitus inadequate control at 2.5%. The death counts are not reported in the registry record. The posted safety information should therefore be read as descriptive event reporting, not as a complete causal assessment.

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

The posted primary results do not establish a clear difference in mean DAS28-CRP AUC between the two randomized rituximab retreatment courses. The unadjusted recalculation estimates a mean difference of -95.4, but its 95% confidence interval extends from -1479.0 to 1288.0. The sponsor-reported adjusted interval also includes zero. Both estimates therefore leave substantial uncertainty about the direction and size of the difference.

The results do not establish that the retreatment courses are exactly equal. A non-significant result is not proof of no difference, and a confidence interval containing zero is compatible with differences in either direction. Nor can the registry’s non-inferiority or equivalence classification be independently assessed without the prespecified margin and analysis details, which are not reported in the registry record.

The comparison is specifically between one and two additional rituximab infusions among people who had received initial rituximab treatment and met the stated response condition at Week 24. It does not estimate the effect of rituximab versus another drug or no treatment. The primary analysis also concerns the per-protocol population, so it should not automatically be generalized to all 224 enrolled participants.

DAS28-CRP AUC summarizes measured disease activity across time. It does not communicate every participant’s experience, each visit’s score, or every aspect of rheumatoid arthritis. The secondary outcome set includes response thresholds and timing measures, but the numerical results for most of those measures are not reported in the registry record. The safety counts are descriptive and do not establish causation.

Overall, the posted data support a cautious reading: the primary estimates are uncertain, and the registry record lacks some details needed to evaluate the adjusted non-inferiority or equivalence analysis, missing-data handling, and multiplicity. They do not justify broad conclusions beyond the particular randomized retreatment comparison and endpoints reported.

18. Why This Trial Matters Statistically

This study illustrates an important distinction between a treatment comparison and a comparison of treatment strategies after an initial response. Participants first received rituximab, and the randomized question concerned the number of additional infusions for those who demonstrated a moderate or good response at Week 24. The result therefore applies to a defined stage of treatment rather than to an initial choice between unrelated therapies.

The primary endpoint also demonstrates why repeated-measure summaries require careful interpretation. An AUC combines values across time and can represent accumulated disease activity, but it can conceal different trajectories that yield similar overall summaries. The visit schedule, actual assessment dates, and endpoint handling at Week 104 are part of what gives the measure its meaning.

Statistically, the result highlights the difference between an estimate and its precision. The point estimate of the unadjusted difference is close to zero relative to a wide interval. The interval conveys more than a single estimate: it indicates that the data do not tightly determine the direction or magnitude of the difference. A p-value alone would not convey that uncertainty.

The record also illustrates why a registry-reported analysis should be read alongside the analysis specification. The adjusted analysis is categorized as non-inferiority or equivalence type, but the margin, method, and decision rule are not reported. Without them, readers cannot assess what conclusion the design was intended to support. Clear reporting of populations, missing-data procedures, multiplicity handling, and analysis methods is central to interpreting clinical trial 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.

The main limitation of the posted efficacy result is its imprecision. The primary unadjusted confidence interval is wide and includes differences favoring either randomized retreatment course. The endpoint analysis includes 51 participants in Arm A and 49 in Arm B, and the registry does not give the reasons that the primary per-protocol counts differ from the secondary weighted-time counts.

The adjusted sponsor analysis is difficult to assess independently because its method, covariates, and estimand are not reported in the registry record. Although it is classified as a non-inferiority or equivalence type result, the margin and decision rule are also not reported. The adjusted estimate should therefore not be interpreted as proof of non-inferiority or equivalence on the basis of the classification alone.

The study was unmasked. The registry record does not provide details about allocation concealment, random-sequence generation, or procedures to minimize assessment bias. It does not report the original sample-size justification, interim analyses, complete statistical analysis plan, or multiplicity strategy. The absence of these details in the registry limits assessment; it does not establish that the procedures were not used.

The primary analysis is per protocol rather than all randomized participants, as the registry defines it. Exclusions for major protocol violations and sensitivity analyses are not described. The record gives a Week 104 extrapolation approach, but fuller missing-data methods and sensitivity analyses are not reported. Most secondary outcome estimates are also not available in the registry record, preventing a comprehensive assessment of consistency across the many listed outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: SMART Study: A Study of Re-treatment With MabThera (Rituximab) in Patients With Rheumatoid Arthritis Who Have Failed on Anti-TNF Alfa Therapy — NCT01126541.
• Registry record last updated 2014-09-15; status last verified 2014-09.
• Results first posted 2014-09-15.
• 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

NCT01126541 is the completed Phase 3 SMART study of rituximab retreatment in rheumatoid arthritis after inadequate response or intolerance to anti-TNF therapy. The randomized comparison was one versus two additional 1000 mg intravenous rituximab infusions at Week 24 after an initial course. The primary endpoint was Week 104 DAS28-CRP AUC in the per-protocol population.

The unadjusted recalculated mean difference was -95.4, with a 95% confidence interval from -1479.0 to 1288.0. The registry-reported adjusted difference was 51.38, with a 95% confidence interval from -131.22 to 233.98, but the method and non-inferiority or equivalence margin are not reported. The estimates are uncertain and do not establish exact equivalence. Safety counts are descriptive, and fuller analysis details are not reported in the registry record.