A Study to Evaluate the Safety and Efficacy of Rituximab in Combination With Methotrexate Compared to Methotrexate Alone in Patients With Active Rheumatoid Arthritis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the Safety and Efficacy of Rituximab in Combination With Methotrexate Compared to Methotrexate Alone in Patients With Active Rheumatoid Arthritis (NCT00299130), a randomized phase 3 study. The primary outcome is Percentage of Participants With American College of Rheumatology (ACR) 20 Response at Week 24.

2. Clinical Question

The trial focuses on whether adding rituximab to methotrexate is associated with different Week 24 response rates than methotrexate with placebo. It also includes two rituximab dose groups, allowing each combination group to be described separately against the same comparator. These comparisons do not, by themselves, establish that the doses differ from each other; a direct dose-to-dose analysis is not reported in the registry record.

The ACR20 outcome is a composite response measure rather than a direct measure of a single symptom or laboratory value. Participants had to meet its joint-count requirements and satisfy a threshold on additional disease assessments. The endpoint therefore addresses a defined pattern of improvement across several components, not every aspect of rheumatoid arthritis or each participant’s experience.

3. Trial Design

The registry record identifies NCT00299130 as a completed phase 3 study with randomized allocation, double masking, and a parallel-group model. Its official title describes a randomized, placebo-controlled, double-blind, parallel-group, international study. The record lists an enrollment of 511 and identifies rheumatoid arthritis as the condition studied.

The three arms were placebo plus methotrexate, rituximab 2 x 0.5 g plus methotrexate, and rituximab 2 x 1.0 g plus methotrexate. In the rituximab groups, the initial infusions were scheduled on Days 1 and 15. The arm descriptions say that, after Week 24, participants could receive further rituximab courses every 24 weeks for up to 5 years if they were not in clinical remission and met safety criteria. The placebo group could switch to rituximab from Week 16 onwards under stated remission and safety conditions. These later treatment provisions matter when interpreting outcomes beyond the initial comparison period; the primary endpoint is measured at Week 24.

The record lists folate, methotrexate, methylprednisolone, placebo, and rituximab as interventions. More detailed administration information is not reported in the registry record’s available arm descriptions. The study start is listed as 2005-10, primary completion as 2008-06, and status as completed.

For the primary endpoint, the registry describes an intent-to-treat population that included randomized participants who received at least 1 or part of an infusion. Its endpoint description says that each ACR component used last observation carried forward values. Participants who withdrew before Week 24, received rescue therapy, or lacked sufficient data to calculate a clinical response were classified as non-responders. The posted endpoint arm counts are 172 for placebo plus methotrexate, 167 for rituximab 2 x 0.5 g plus methotrexate, and 170 for rituximab 2 x 1.0 g plus methotrexate. A fuller account of randomization procedures, allocation concealment, and the trial’s original statistical plan is not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: Of the 509 participants, one participant was randomized first to rituximab 2 x 1.0 g + MTX and then to rituximab 2 x 0.5 g + MTX. No assessments were recorded or medication given after first randomization and all data used in analyses was following the second randomization; hence, participant is included only in rituximab 2 x 0.5 g + MTX arm.

Treatment Period (up to 5 Years)

Reasons for not completing this period:

Safety Follow-up (SFU) (48 Weeks)

Reasons for not completing this period:

Extended SFU (ESFU) (up to 5.1 Years)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to treat population included all randomized participants who received at least 1 or part of an infusion. ACR was calculated using the last observation carried forward (LOCF) values for each component. Participants who withdrew prior to week 24, received rescue therapy or had insufficient data to calculate ACR were considered non-responders.

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: Safety population included all randomized participants who received any part of an infusion.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With American College of Rheumatology (ACR) 20 Response at Week 24, measured over Baseline and Week 24.

The primary endpoint is the percentage of participants with an ACR20 response at Week 24, measured from baseline. Under the registry definition, an ACR20 response requires at least a 20% improvement from baseline in both tender joint count and swollen joint count, along with a 20% improvement in three of five additional measures. These are physician’s global assessment, patient’s global assessment, patient’s pain assessment, the Health Assessment Questionnaire, and an acute-phase reactant: C-reactive protein or, if that was missing, erythrocyte sedimentation rate.

This composite is used to represent improvement across multiple features of rheumatoid arthritis rather than relying on a single measure. Requiring improvement in joint counts and several other assessments gives the response a structured, threshold-based meaning. It is still a binary classification: a participant either meets the stated criteria or does not. The endpoint does not describe the magnitude of improvement beyond the threshold, nor does it show the result for each component separately.

The registry endpoint description specifies that participants who withdrew before Week 24, received rescue therapy, or had insufficient data to calculate a response were treated as non-responders. It also states that last observation carried forward values were used for each component. Those choices affect how missing or post-rescue observations contribute to the response classification and should be kept in mind when interpreting the reported percentages.

7. Results Posted in the Registry

• Rituximab 2 x 0.5 g + MTX: 54.5% (91/167) versus 23.3% (40/172) on control; risk difference 31.2 percentage points (95% CI 21.4 to 41.1), risk ratio 2.34 (1.73–3.18); unadjusted two-proportion z-test p = <0.001.
• Rituximab 2 x 1.0 g + MTX: 50.6% (86/170) versus 23.3% (40/172) on control; risk difference 27.3 percentage points (95% CI 17.5 to 37.1), risk ratio 2.18 (1.60–2.96); 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 With an ACR50 Response at Week 24

• 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:
  • Rituximab 2 x 0.5 g + MTX: 26.3% (44/167) versus 9.3% (16/172) on control; risk difference 17.0 percentage points (95% CI 9.1 to 25.0), risk ratio 2.83 (1.67–4.82); unadjusted two-proportion z-test p = <0.001.
  • Rituximab 2 x 1.0 g + MTX: 25.9% (44/170) versus 9.3% (16/172) on control; risk difference 16.6 percentage points (95% CI 8.7 to 24.5), risk ratio 2.78 (1.64–4.73); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Rituximab 2 x 0.5 g + 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 proportion with the event is statistically higher for Rituximab 2 x 1.0 g + MTX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With an ACR70 Response at Week 24

• 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:
  • Rituximab 2 x 0.5 g + MTX: 9.0% (15/167) versus 5.2% (9/172) on control; risk difference 3.7 percentage points (95% CI -1.7 to 9.2), risk ratio 1.72 (0.77–3.81); unadjusted two-proportion z-test p = 0.178.
  • Rituximab 2 x 1.0 g + MTX: 10.0% (17/170) versus 5.2% (9/172) on control; risk difference 4.8 percentage points (95% CI -0.8 to 10.4), risk ratio 1.91 (0.88–4.17); unadjusted two-proportion z-test p = 0.096.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rituximab 2 x 0.5 g + MTX and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rituximab 2 x 1.0 g + MTX and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Disease Activity Score (DAS28-ESR) at Week 24

• 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:
  • Rituximab 2 x 0.5 g + MTX: mean -1.71 versus -0.76 on control; difference -0.95 (95% CI -1.23 to -0.67), standardized effect d = -0.72; z-test p = <0.001.
  • Rituximab 2 x 1.0 g + MTX: mean -1.68 versus -0.76 on control; difference -0.92 (95% CI -1.20 to -0.64), standardized effect d = -0.70; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Rituximab 2 x 0.5 g + 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 Rituximab 2 x 1.0 g + MTX than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span stricter ACR response thresholds, a disease activity score, EULAR response, joint counts, and patient assessments. Together, they cover related aspects of disease response using both threshold-based classifications and continuous measurements. The posted ACR50 and DAS28-ESR summaries follow a direction broadly consistent with the primary ACR20 pattern, while the ACR70 comparisons are less precise. These secondary observations give context, but they are not the same endpoint as the primary response.

Secondary outcomes can help assess whether a primary finding appears alongside changes in related measures. Agreement across different measures may make the pattern easier to understand, while differences can reflect distinct definitions, scales, and response thresholds. However, the endpoints are not interchangeable: a responder classification, an average score change, and a joint-count change describe different features of the trial data. The primary result remains the designated Week 24 ACR20 comparison.

Unadjusted secondary results carry less weight because multiple outcomes and comparisons create more opportunities for apparently notable findings. Without a reported testing hierarchy or multiplicity adjustment, the registry record does not establish which secondary comparisons were confirmatory or how repeated testing was handled. Their unadjusted p-values should not be treated as if each were the only statistical test conducted.

The record lists other secondary measures, including EULAR response, swollen and tender joint counts, patient global assessment, and pain assessment. Their numerical results are not reported in the registry record figures described for this analysis. The absence of those results should not be interpreted as evidence of no change; it means their findings cannot be characterized from the available summaries. The secondary evidence is therefore supportive and incomplete, and should be read alongside the endpoint definitions and the limitations of unadjusted comparisons.

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

• Percentage of Participants With an ACR50 Response at Week 24
• Percentage of Participants With an ACR70 Response at Week 24
• Change From Baseline in Disease Activity Score (DAS28-ESR) at Week 24
• Percentage of Participants With European League Against Rheumatism (EULAR) Response at Week 24
• Percent Change From Baseline in Swollen Joint Count
• Percent Change From Baseline in Tender Joint Count
• Percent Change From Baseline in Patient's Global Assessment of Disease Activity
• Percent Change From Baseline in Patient's Pain Assessment

9. Statistical Interpretation

10. Statistical Methods Explained

The endpoint is binary: each participant is classified as meeting or not meeting the ACR20 definition. For a binary outcome, a response percentage describes the share of the arm classified as responders. Comparing two such percentages can be summarized by a risk difference, which expresses the difference between the response proportions on the proportion scale. A value of zero would represent equal proportions in the comparison. The posted unadjusted risk-difference estimates compare each rituximab-plus-methotrexate arm with placebo plus methotrexate.

How should the confidence interval be read?

A confidence interval describes the statistical uncertainty around an estimate under the assumptions of the method used. A relatively narrower interval indicates greater precision than a wider interval, while a wider interval leaves a broader range of values compatible with the data and method. The intervals for the primary comparisons are recalculations from posted summary counts. They are not reported adjusted-model intervals, and their interpretation depends on the unadjusted comparison method.

The posted p-values for the primary comparisons are also unadjusted recalculations. A p-value is a measure of how compatible the observed data are with a specified null hypothesis under a statistical model; it is not the probability that the null hypothesis is true, nor a measure of clinical importance. A small p-value does not describe the size or precision of a difference on its own, so it should be considered alongside the estimated risk difference and its interval. The registry record does not report the statistical procedure used for its own primary analysis.

What does unadjusted mean?

An unadjusted comparison uses the posted outcome counts without accounting for covariates or other model terms. This gives a transparent summary of the observed arm-level proportions, but it is not necessarily identical to a sponsor’s planned analysis. The calculations do not incorporate details that are not available in the registry record, such as stratification, covariate adjustment, or other features of a prespecified model. The registry record does not report those analysis details.

Randomization is intended to make treatment groups comparable on average, but a description of random allocation does not reveal every implementation detail or ensure that every realized group is identical in all measured and unmeasured characteristics. An unadjusted calculation is therefore a descriptive comparison of the posted groups. It should not be relabeled as an adjusted treatment effect.

How is the responder definition used?

ACR20 combines joint-count changes with changes in additional disease assessments. Participants need to satisfy the required improvement in both tender and swollen joint counts, as well as the required improvement in three of the listed five measures. The outcome thus makes a single responder classification from multiple inputs. A participant who does not meet the full set of criteria is not counted as an ACR20 responder, even if some individual measures improved.

The registry definition applies last observation carried forward to each component. In general, last observation carried forward uses an earlier recorded value in place of a missing later value. This approach can make the analysis depend on assumptions about what would have happened after the last observed measurement; those assumptions may not match actual subsequent outcomes. The record further specifies non-responder classification for participants who withdrew before Week 24, received rescue therapy, or had insufficient information to calculate a response. Those rules are part of the endpoint interpretation, not optional additions to the displayed response rates.

How should the secondary measures be understood?

The secondary outcomes include ACR50 and ACR70 response, change in DAS28-ESR, EULAR response, and changes in swollen and tender joint counts and patient assessments. Binary response measures use responder thresholds, while a mean change measure summarizes the average change on its scale. These outcome types answer related but distinct questions. ACR20 is the designated primary outcome in the registry record; secondary findings offer supporting context rather than replacing that primary endpoint.

Where recalculated secondary comparisons are displayed, they are unadjusted and should be treated as exploratory summaries unless a prespecified analysis plan establishes otherwise. The registry record does not report the statistical analysis plan or a multiplicity procedure. No claim about the sponsor’s intended model, testing hierarchy, interim analyses, or sample-size justification can be made from the available record.

What are the limits of these calculations?

The calculations rely on the counts and summary values posted for each outcome. They do not reconstruct participant-level data, check the trial database, or account for unreported covariates and analysis decisions. The primary endpoint percentages and recalculated comparison summaries may also use values at different displayed precision, so minor differences in the last digit can occur when rounded values are compared. No additional precision beyond the registry figures is warranted.

These methods explain statistical summaries, not clinical recommendations. Statistical evidence concerns the comparison and outcome definition used; it does not establish every benefit, risk, or longer-term outcome. Interpretation also depends on the population, follow-up period, treatment conditions, and missing-data rules recorded for each analysis.

11. Confidence Intervals and Precision

The primary risk-difference estimate for rituximab 2 x 0.5 g plus methotrexate versus placebo plus methotrexate is 0.312, with a 95% confidence interval from 0.214 to 0.411. For rituximab 2 x 1.0 g plus methotrexate versus placebo plus methotrexate, the estimate is 0.273, with a 95% confidence interval from 0.175 to 0.371. These are unadjusted recalculations from the posted counts.

In general, a confidence interval gives a range of values that are compatible with the data and the method under its assumptions. It is not a guarantee that the true value lies inside the particular interval, and it does not describe variation among individual participants. The interval width is useful for judging precision: narrower intervals indicate less statistical uncertainty than wider intervals. Both primary intervals are above zero, but their range still matters when considering the plausible size of the risk difference.

Precision is influenced by the amount of information in the comparison and by the outcome’s variability. The primary arm counts are 172, 167, and 170; the interval estimates reflect those posted groups and the recalculation method. The registry record does not provide an adjusted confidence interval or enough detail to reproduce a sponsor’s analysis. The interval should consequently be understood as an unadjusted summary, not as a definitive account of every analysis the trial may have conducted.

Confidence intervals also do not address multiplicity. When many endpoints or comparisons are examined, the chance of at least one apparently notable result can increase unless the analysis plan accounts for repeated testing. A separate adjustment or testing hierarchy is not reported in the registry record. The primary endpoint is distinguished from secondary outcomes by its designation in the record, but that designation alone does not disclose the planned multiplicity strategy.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are participants per arm for the two-arm comparison, not total participants across arms and not total events. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% probability of detecting the specified effect under the stated assumptions, if that effect and the assumptions are correct. The 90% power column gives the corresponding planning figure for a 90% probability. These figures are planning illustrations, not observed power; observed power is not a way to establish whether the trial result is reliable.

Rows based on 100% of the observed effect use the full estimated effect from the posted comparison. Rows based on 75% or 50% of the observed effect consider smaller effects. Smaller effects are harder to distinguish from random variation, so they require more participants per arm to reach the same target power under the same assumptions. This relationship is visible across the planning illustrations for the primary endpoint and the secondary comparisons.

These figures should not be interpreted as the number originally enrolled or as evidence that the completed trial was designed around the observed effects. They do not incorporate any unreported design features, dropout allowance, interim monitoring, or analysis adjustments. The figures are useful for illustrating how assumed effect size and desired power influence planning, but they do not replace a trial-specific sample-size calculation based on prespecified assumptions.

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 = 0.233; treatment proportion p₁ = 0.545; average p̄ = 0.389.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6894 = 1.3512.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6530 = 0.5496.
4. n = (1.3512 + 0.5496)² / (0.3124)² = 37.0, rounded up to 38 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 <- 0.232558139534884                          # control proportion
p1 <- 0.544910179640719                          # 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(299130)
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 = 38 (80% power), 50 (90% power)
 75% of observed effect: n per arm = 64 (80% power), 85 (90% power)
 50% of observed effect: n per arm = 137 (80% power), 183 (90% power)
power.prop.test: 37 
Simulated power at n = 38 per arm: 0.809 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines more than one outcome, comparison, time point, or analysis. If each test is considered separately without accounting for the number of tests, the overall chance of obtaining at least one small p-value by chance can be greater than the chance for an isolated test. This is a general statistical issue, not evidence that any particular finding in this trial is false.

The registry record identifies ACR20 at Week 24 as the primary endpoint and lists multiple secondary outcomes, including ACR50, ACR70, DAS28-ESR, EULAR response, joint counts, and patient assessments. The record reports no analyses in its analysis field, and a detailed statistical analysis plan or multiplicity adjustment is not reported in the registry record. It is therefore not possible to determine from this information whether the trial used a hierarchy, adjusted thresholds, or other safeguards for multiple testing. The primary endpoint’s designation does not, on its own, disclose the testing strategy.

Missing data are addressed explicitly in the primary endpoint description. Each ACR component was calculated using last observation carried forward values. Participants who withdrew before Week 24, received rescue therapy, or had insufficient data to calculate clinical response were counted as non-responders. This defines how those cases contribute to the reported binary outcome, but it does not eliminate uncertainty about the unobserved measurements.

In general, missing-data methods make assumptions about outcomes that were not observed. Carrying a prior measurement forward assumes that value is an appropriate substitute for the later one; classifying specified cases as non-responders assigns them to the non-response category. Different assumptions can affect response percentages, particularly if the reasons for missingness are related to outcome. The registry record does not report sensitivity analyses or other missing-data approaches for this endpoint.

The primary analysis population is described as randomized participants who received at least 1 or part of an infusion. A fuller account of analysis populations for secondary outcomes, or of how participants were handled in analyses beyond the stated primary rules, is not reported in the registry record. These gaps limit how fully the posted results can be compared with a prespecified analysis plan.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: osteoarthritis (2.9%), fall (2.4%), myocardial infarction (2.4%), pneumonia (2.4%), angina pectoris (2.3%).

The serious adverse-event figures are counts of affected participants among those at risk in each posted group. For the initial placebo plus methotrexate group, the record reports 16 affected among 172 at risk. For rituximab 2 x 0.5 g plus methotrexate, it reports 52 among 167; for the rituximab 1.0 g plus methotrexate group, it reports 46 among 170. These are descriptive counts, not estimates of causation.

The record also lists separate switch-population and extended safety follow-up groups. Those group labels refer to different follow-up categories and should not be combined with the initial treatment groups as though they were a single set of observations. Serious-event terms listed among the most frequent include osteoarthritis, fall, myocardial infarction, pneumonia, angina pectoris, and hypoglycaemia. The percentages attached to those terms are registry summaries; they do not establish that a treatment caused the event.

Deaths are not reported in the registry record’s adverse-event summaries. The figures alone do not describe event timing, severity beyond the serious-event classification, or comparative risk over equivalent follow-up. They should be read as safety reporting summaries rather than as a complete assessment of treatment risks.

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

The Week 24 primary result describes the percentage meeting a specific ACR20 response definition in each randomized arm. The posted percentages are higher in both rituximab-plus-methotrexate groups than in the placebo-plus-methotrexate group, and the unadjusted recalculated risk-difference intervals are above zero. This is a statistical description of the trial’s posted endpoint summaries, with uncertainty represented by the confidence intervals.

The result does not establish that every participant experienced improvement, that all disease features changed in the same way, or that the size of the response was the same for all participants who met the threshold. ACR20 is a composite binary classification. It does not provide the distribution of individual component changes or show how far responders exceeded the response threshold.

The findings also do not establish a difference between the two rituximab doses. Each dose group is compared with placebo plus methotrexate, while a direct comparison between rituximab groups is not reported in the registry record. Numerical differences between the two arm summaries alone are not a substitute for a direct statistical comparison.

The interpretation is limited to the Week 24 outcome, the populations and endpoint rules recorded, and the unadjusted recalculations described. Participants who withdrew before Week 24, received rescue therapy, or lacked sufficient data were classified as non-responders, and last observation carried forward was used for ACR components. The record does not report the full statistical plan or a multiplicity strategy. Longer-term treatment provisions, including switching and further courses, also mean that later follow-up would address a different treatment context.

These results do not by themselves establish how the findings apply to people outside the enrolled study population or under different treatment conditions. Statistical summaries are not medical advice and do not resolve an individual treatment decision. They describe the comparison and measurements recorded in this completed trial, with the limitations of the registry information and analysis detail kept in view.

17. Why This Trial Matters Statistically

This trial illustrates how a clinical outcome can be framed as a threshold-based responder definition and compared across randomized groups. The ACR20 endpoint combines joint counts with additional assessments, so its interpretation depends on understanding both the component criteria and the rule used to classify missing or post-rescue cases. A percentage without that endpoint definition would be difficult to interpret meaningfully.

It also shows why effect estimates and uncertainty should be read together. The unadjusted risk differences describe the magnitude of the observed comparisons on the proportion scale, while their confidence intervals show the range of values compatible with the data and the calculation method. P-values alone would not communicate this range or the estimated size of the difference.

The two active-dose comparisons share one placebo-plus-methotrexate comparator. This makes the comparisons easy to describe, but it does not supply a direct test of the two active doses against each other. A statistical reader should distinguish each comparison that is actually reported from other comparisons that might seem natural from the arm structure.

The record also demonstrates the importance of transparency about analysis plans. Multiple secondary endpoints are listed, yet the analysis field reports no analyses and the multiplicity strategy is not reported. Missing-data rules are described for the primary endpoint, but sensitivity analyses are not reported. Those details affect how strongly secondary findings can be interpreted and how robust the primary result appears under alternative assumptions.

Finally, the sample-size illustrations connect observed effects with hypothetical future planning assumptions, rather than reconstructing the original design. Distinguishing planning calculations from the trial’s actual design and from observed results is essential to avoid treating a post hoc illustration as evidence about the trial’s original power or intent.

18. 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 does not report the full statistical analysis plan, the trial’s original sample-size justification, interim analyses, or a multiplicity procedure. These omissions prevent confirmation of the planned analysis model, any prespecified testing hierarchy, and how the reported comparisons relate to the sponsor’s intended analyses.

The primary endpoint uses last observation carried forward values for ACR components and classifies participants who withdrew before Week 24, received rescue therapy, or had insufficient data as non-responders. These rules are specified, but sensitivity analyses using alternative missing-data assumptions are not reported in the registry record. The effect of those choices on the reported response rates therefore cannot be assessed from these summaries alone.

The posted comparisons are unadjusted recalculations from group summaries. The record does not report covariate-adjusted estimates for these comparisons, and no direct comparison between the two rituximab dose groups is reported. The primary outcome is at Week 24; later treatment could include switching in the placebo group and further rituximab courses in the other groups, limiting simple interpretation of longer-term contrasts from the initial assignment.

Several secondary outcomes are listed, but numerical results for all listed measures are not included in the available summaries. The safety information includes counts for several groups and follow-up categories, but deaths are not reported in the registry record, and the summaries do not provide full detail on event timing or comparative exposure. These limitations constrain what can be concluded from the registry summaries without implying that unreported analyses or outcomes were absent from the trial itself.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study to Evaluate the Safety and Efficacy of Rituximab in Combination With Methotrexate Compared to Methotrexate Alone in Patients With Active Rheumatoid Arthritis — NCT00299130.
• Registry record last updated 2017-04-17; status last verified 2017-03.
• Results first posted 2013-06-28.
• 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.

22. Record Summary

NCT00299130 is a completed phase 3 randomized, double-blind, parallel-group study in active rheumatoid arthritis. It compared placebo plus methotrexate with two rituximab-plus-methotrexate groups. The primary outcome was ACR20 response at Week 24.

The posted primary response percentages were 23.3 for placebo plus methotrexate, 54.5 for rituximab 2 x 0.5 g plus methotrexate, and 50.6 for rituximab 2 x 1.0 g plus methotrexate. Unadjusted recalculations report risk-difference estimates of 0.312 and 0.273, respectively, with both p-values < 0.001. The registry record specifies last observation carried forward for ACR components and non-responder classification for certain withdrawals, rescue therapy, or insufficient data.

The record also lists multiple secondary outcomes and safety summaries. A detailed statistical plan, multiplicity strategy, and original sample-size justification are not reported in the registry record. Interpretations should remain tied to the Week 24 endpoint, its stated analysis rules, and the unadjusted comparisons.