A Study of Tocilizumab and Methotrexate Treatment Strategies (Adding Tocilizumab to Methotrexate Versus Switching to Tocilizumab) in Patients With Active Rheumatoid Arthritis With Inadequate Response to Prior Methotrexate Treatment: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Tocilizumab and Methotrexate Treatment Strategies (Adding Tocilizumab to Methotrexate Versus Switching to Tocilizumab) in Patients With Active Rheumatoid Arthritis With Inadequate Response to Prior Methotrexate Treatment (NCT00810199), a randomized phase 3 study. The primary outcome is Percentage of Participants With Disease Activity Score 28 Joints (DAS28) Remission at Week 24.

2. Clinical Question

The comparison focuses on whether continuing methotrexate alongside tocilizumab is associated with a different rate of DAS28 remission than using tocilizumab with placebo instead of methotrexate. Both strategies include tocilizumab, so the main contrast is the accompanying methotrexate strategy rather than tocilizumab versus no tocilizumab.

The study was described as enrolling people with moderate to severe rheumatoid arthritis whose response to prior methotrexate was inadequate. The registry record also describes possible treatment adjustments after the first 24 weeks, based on response. The primary question concerns the Week 24 remission endpoint, before the later period in which the treatment intensity could be adjusted.

The result should be read as a comparison of the strategies and the outcome as defined in the record. It does not by itself establish what would happen with other patient groups, other treatment strategies, or outcomes not measured in the trial.

3. Trial Design

The registry record identifies this as a Phase 3, randomized, parallel-group study with quadruple masking. It is marked completed. The recorded enrollment is 556, while the primary outcome arm counts are 277 for tocilizumab plus methotrexate and 276 for tocilizumab plus placebo. The record does not explain the difference between the enrollment figure and the outcome counts.

Both arms received tocilizumab intravenously every 4 weeks. During the first 24 weeks, one arm also received weekly oral methotrexate and the other weekly oral placebo. The descriptions state that participants continued their pre-study methotrexate dose in the active-methotrexate arm. They also state that participants taking oral corticosteroids remained on their pre-study dose, up to 10 mg/day. These details describe the recorded regimen; further details about how treatment was managed for individual participants are not reported in the registry record.

After the first 24 weeks of blinded treatment, the brief summary says that treatment adjustments, including increases or decreases in treatment intensity, could be introduced at intervals based on response. The anticipated time on study treatment was up to 3 years. The posted primary outcome is assessed at Week 24, and the registry also includes later outcomes.

The record lists a target sample size of approximately 470 in the brief summary, while the enrollment field records 556. The original sample-size justification and the assumptions used to set that target are not reported in the registry record. The trial dates recorded are a start in 2009-03 and primary completion in 2010-08. Details such as the randomization procedure, allocation concealment, the specific roles covered by quadruple masking, and the reasons for any differences between target and recorded enrollment are 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.

Overall Study

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 study drug.

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: Baseline measures are based on the Safety Population and include all randomized participants who received at least one dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Disease Activity Score 28 Joints (DAS28) Remission at Week 24, measured over Week 24.

The primary endpoint is the percentage of participants with DAS28 remission at Week 24. DAS28 combines tender joint count and swollen joint count across 28 joints, the participant’s global assessment of disease activity on a visual analog scale, and erythrocyte sedimentation rate. The registry describes a possible score from 0 to approximately 10. It identifies scores below 2.6 as indicating the best disease control and scores above 5.1 as indicating worse disease control. Remission is defined as a score < 2.6.

A percentage endpoint expresses how often the defined outcome occurred in each treatment group. It is useful for a binary outcome such as whether a participant met the remission threshold by a specified time. The threshold makes the endpoint straightforward to interpret, but it also reduces a continuous disease-activity score to a yes-or-no classification. Participants with scores close to the threshold may be classified differently despite similar underlying scores.

The Week 24 timing makes the endpoint a comparison at the end of the initial blinded treatment period described in the record. It does not capture the full course of disease activity or later changes in treatment. The primary analysis population is described as randomized participants who received study drug. How missing Week 24 measurements were handled is not reported in the registry record.

7. Results Posted in the Registry

• Tocilizumab + Methotrexate: 40.4% (112/277) versus 34.8% (96/276) on control; risk difference 5.7 percentage points (95% CI -2.4 to 13.7), risk ratio 1.16 (0.94–1.44); unadjusted two-proportion z-test p = 0.170.

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.

Area Under Curve (AUC) DAS28

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Tocilizumab + Methotrexate: mean 3.97 versus 4.23 on control; difference -0.26 (95% CI -0.52 to 0.00), standardized effect d = -0.17; z-test p = 0.053.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tocilizumab + Methotrexate and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Disease Activity Score 28 (DAS28) Remission

• 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:
  • Tocilizumab + Methotrexate: 45.5% (126/277) versus 36.6% (101/276) on control; risk difference 8.9 percentage points (95% CI 0.7 to 17.1), risk ratio 1.24 (1.02–1.52); unadjusted two-proportion z-test p = 0.034.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Tocilizumab + Methotrexate than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Who Withdrew Due to Lack of Sufficient Therapeutic Response

• 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:
  • Tocilizumab + Methotrexate: 1.8% (5/277) versus 4.7% (13/276) on control; risk difference -2.9 percentage points (95% CI -5.9 to 0.0), risk ratio 0.38 (0.14–1.06); unadjusted two-proportion z-test p = 0.054.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tocilizumab + Methotrexate and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add information across different measures and times, but they do not replace the primary Week 24 endpoint. Taken together, the posted results generally point in the direction of more favorable values for the methotrexate strategy on the outcomes with reported comparisons. The pattern is not uniform in statistical precision: some sponsor analyses have intervals that exclude their null value, while other comparisons remain compatible with no difference.

These endpoints address different aspects of the treatment strategies. The continuous DAS28 area-under-the-curve outcome describes disease activity across Baseline to Week 24, while later remission and withdrawal outcomes address other time points or events. They cannot be treated as repeated measurements of precisely the same question. Treatment adjustments could be introduced after the initial blinded period, which is relevant when interpreting outcomes beyond Week 24.

The registry lists ACR20, ACR50, ACR70, and ACR90 response outcomes, as well as time to first response at those thresholds. Results for those measures are not reported in the registry record. The record lists 35 secondary outcomes, but detailed results for most of those outcomes are not included in the available result details.

Multiple secondary outcomes create a multiplicity concern: the more comparisons considered, the greater the opportunity for chance findings to appear notable. Whether the trial prespecified a multiplicity adjustment, a hierarchy among endpoints, or a strategy for interpreting secondary outcomes is not reported in the registry record. Accordingly, secondary findings should be treated as supporting context, not as a substitute for the primary result or as a collection of independent confirmations.

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

• Percentage of Participants With American College of Rheumatology (ACR20) Response
• Percentage of Participants With ACR50 Response
• Percentage of Participants With ACR70 Response
• Percentage of Participants With ACR90 Response
• Time to First ACR20 Response
• Time to First ACR50 Response
• Time to First ACR70 Response
• Time to First ACR90 Response

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help place these results in context. The primary outcome is binary: each participant either met the DAS28 remission definition at Week 24 or did not. A group percentage describes the proportion meeting that definition. Comparing percentages can be done through a risk difference, while logistic regression and the Cochran-Mantel-Haenszel method can express a comparison as an odds ratio. These measures answer related but distinct questions and need not have the same numerical value.

What does a risk difference mean?

A risk difference subtracts one group’s event proportion from the other’s. For the primary endpoint, the recalculated value is 0.057, with the methotrexate arm as the first group in the comparison. It is expressed on the proportion scale, not as an odds ratio. A positive estimate indicates a higher observed remission proportion in the methotrexate arm, while a negative estimate would indicate a lower observed proportion. Its confidence interval ranges from -0.024 to 0.137, so the data do not rule out differences in either direction.

Why report an odds ratio?

An odds ratio compares the odds of the outcome between groups. An odds ratio of 1 represents equal odds; a value above 1 indicates higher odds in the group named first in the comparison, and a value below 1 indicates lower odds. Odds are not the same as probabilities, so an odds ratio should not be read as a percentage-point increase. Logistic regression estimates an odds ratio through a model, while the Cochran-Mantel-Haenszel method provides a stratified comparison when the relevant strata and analysis details are specified. Those strata and the full model specifications are not reported in the registry record.

The sponsor’s primary analysis reports results from both methods. Their confidence intervals include 1 and their p-values are 0.205 and 0.189. In general, a confidence interval for an odds ratio that includes 1 does not exclude equal odds at the corresponding confidence level. A p-value summarizes how incompatible the observed data are with a stated null model under the analysis assumptions; it is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect.

Why do analysis methods give different estimates?

Different methods can use different scales, covariate adjustments, or stratification and therefore yield somewhat different estimates. A simple recalculation from group counts is unadjusted. A model-based analysis may account for features specified in its model. The registry gives method names and estimates but does not report enough detail to reconstruct every modeling choice. Consequently, the unadjusted risk difference and the sponsor’s odds ratios should be understood as complementary descriptions, not as identical quantities that must match.

For a continuous outcome, such as the area under the DAS28 curve, the analysis can compare group means rather than event proportions. The posted secondary result reports an ANCOVA mean difference of -0.26 with a 95% confidence interval from -0.41 to -0.11 and p < 0.001. ANCOVA generally compares outcomes while accounting for covariates, but the covariates and model specification for this analysis are not reported in the registry record. The recalculated mean difference uses posted summary statistics and is unadjusted; it is not the same estimand as an adjusted ANCOVA result. The calculations also note that the pooled standard deviation is approximated from standard errors, so that recalculation is an approximation.

What does over-dispersion mean in general?

For count or rate outcomes, over-dispersion means that variation in the data exceeds what a simple model assumes. Ignoring it can make uncertainty look too small. The posted primary endpoint is a binary percentage, not a count-rate model, and the registry does not report use of an over-dispersion adjustment. The concept is relevant when choosing models for other data structures, but no claim about over-dispersion in this trial can be made from the recorded results.

Interpretation also depends on the analysis population and missing-data approach. The registry describes the primary population as all randomized participants who received study drug. This is a restricted definition compared with an analysis of everyone randomized, because receiving study drug is an eligibility condition in the stated population. The handling of participants without an outcome measurement, deviations from assigned treatment, and other analysis populations is not reported in the registry record.

Finally, a statistically notable secondary result does not automatically have the same evidential standing as the primary result. Trials often evaluate multiple outcomes or time points. When many comparisons are made, the chance of finding at least one apparently unusual result by chance can increase. The registry record includes many outcome measures and analyses, but whether and how the trial’s own analyses adjusted for multiplicity is not reported in the registry record. Secondary results should therefore be considered alongside the primary endpoint and the prespecified analysis plan, whose details are not reported.

11. Confidence Intervals and Precision

Confidence intervals describe the range of effect estimates compatible with the data under the analysis and its assumptions. They indicate precision as well as direction: a narrower interval reflects less statistical uncertainty than a wider one. They do not guarantee that the true effect lies within the interval, and they do not account for every possible source of bias or model error.

For the primary Week 24 comparison, the unadjusted risk-difference interval runs from -0.024 to 0.137. It includes zero, the value representing no difference in remission proportions. The interval therefore does not identify a single direction of effect with confidence. The sponsor’s odds-ratio intervals, 0.882 to 1.799 and 0.889 to 1.814, both include 1, the equal-odds value. These intervals also allow for uncertainty on either side of the null comparison.

The interval width matters alongside the point estimate. A point estimate can suggest a direction, but its precision determines how much the data narrow the plausible range. The primary results are not precise enough to exclude no difference. This does not establish equality; it indicates that the registry’s analyses leave uncertainty about the direction and size of the underlying difference.

Intervals for secondary outcomes vary by endpoint and analysis. For example, the Week 52 reported odds-ratio intervals are above 1, while the withdrawal comparison’s reported difference interval extends across zero. These secondary intervals should be read in light of the number of outcomes considered and the analysis methods used. A 95% confidence interval is a statistical uncertainty summary for its particular estimate; it is not a direct statement about the probability that a treatment is beneficial or harmful.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations show how many participants per arm would be needed under the stated planning assumptions to detect specified fractions of an observed effect. The rows planning for 100%, 75%, and 50% of the observed effect illustrate how the planning target changes as the effect to detect becomes smaller. Smaller effects generally require more participants to distinguish them from random variation.

The assumptions for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect is the stated fraction of the observed effect. For these binary and continuous outcomes, the entries are participants per arm, not total events. The sample-size assumptions note that time-to-event illustrations, when present, give total events; no such time-to-event planning illustration is included in the results.

The 80% power column represents the number of participants per arm associated with an 80% chance of detecting the assumed effect under the planning model, if that effect and the assumptions are correct. The 90% power column represents the corresponding number for a 90% chance. These are prospective planning quantities, not evidence about how likely the observed result was to be significant after the trial was completed.

These calculations use observed effects as planning inputs. They are illustrations, not the trial’s original design calculations, and they are not observed power. The original design assumptions and sample-size justification are not reported in the registry record. A planning illustration based on a trial’s observed estimate can be especially uncertain when that estimate itself is imprecise.

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 = 0.348; treatment proportion p₁ = 0.404; average p̄ = 0.376.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6850 = 1.3427.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6839 = 0.5756.
4. n = (1.3427 + 0.5756)² / (0.0565)² = 1,152.4, rounded up to 1,153 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 <- 0.347826086956522                          # control proportion
p1 <- 0.404332129963899                          # 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(810199)
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 = 1,153 (80% power), 1,543 (90% power)
 75% of observed effect: n per arm = 2,034 (80% power), 2,723 (90% power)
 50% of observed effect: n per arm = 4,541 (80% power), 6,078 (90% power)
power.prop.test: 1152.4 
Simulated power at n = 1,153 per arm: 0.805 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s own primary analyses as odds ratios from Cochran-Mantel-Haenszel and logistic regression methods. Those analyses give odds ratios of 1.260 and 1.270, with 95% confidence intervals that include 1 and reported p-values of 0.205 and 0.189. They are the trial’s reported inferential analyses for the primary endpoint.

The recalculated result is an unadjusted risk difference of 0.057, with a 95% confidence interval from -0.024 to 0.137 and p = 0.17. It is derived from the posted group summaries and uses a different effect measure and analysis approach. A risk difference and an odds ratio are not numerically interchangeable, and the recalculation does not reproduce the sponsor’s model-based or stratified analyses.

The registry does not flag a discrepancy between the recalculation and sponsor analysis. The sponsor’s reported analyses should nevertheless be treated as the primary trial analyses, while the recalculation provides a transparent, simple comparison based on the posted group values. Both sets of primary results indicate uncertainty rather than a conclusive Week 24 difference.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, comparisons, or time points. Even if each analysis uses a conventional significance threshold, conducting many analyses can increase the chance that at least one result appears statistically notable by chance. The registry record lists 36 outcome measures and 64 analyses, as well as a range of secondary outcomes. Those counts make it important to understand which outcomes were prespecified as primary, how secondary outcomes were prioritized, and whether any adjustment was used.

The primary endpoint is identified as Week 24 DAS28 remission, and the record reports sponsor analyses for it. However, the registry record does not report whether the trial used a formal multiplicity procedure, a hierarchy or gatekeeping plan for secondary outcomes, or a distinction between confirmatory and exploratory comparisons. Without those details, secondary p-values should not be interpreted as if each were the only test conducted.

The primary analysis population is described as the intent-to-treat population including all randomized participants who received study drug. That definition is narrower than a population including every randomized participant regardless of treatment receipt. The registry record does not report the number of participants excluded from this stated population, the reasons for any exclusions, or whether additional analysis populations were used.

Missing outcome data can affect a group comparison if the probability of missingness differs between groups or relates to the outcome. The registry record does not report the amount or pattern of missing primary outcome data, the methods used to handle missing measurements, or sensitivity analyses assessing alternative assumptions. It also does not report details of protocol deviations or how participants who changed or discontinued treatment were handled in each analysis.

These omissions do not establish that the analyses were inadequate; they limit what can be assessed from the registry record. The statistical analysis plan, detailed missing-data procedures, and multiplicity strategy are not reported in the registry record.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (1.1%), bronchopneumonia (1.1%), erysipelas (0.7%), transient ischaemic attack (0.7%), femoral neck fracture (0.7%).

The serious adverse event figures are reported by treatment group: 49 affected participants among 277 at risk in the tocilizumab plus methotrexate group, and 48 among 276 at risk in the tocilizumab plus placebo group. These are counts of participants with serious adverse events, not counts of all serious-event episodes. The registry figures should be read as descriptive group data; they do not alone establish whether the strategies differ in safety.

The listed serious adverse event terms include pneumonia and bronchopneumonia, each reported at 1.1%, along with erysipelas, transient ischaemic attack, femoral neck fracture, and tendon rupture, each reported at 0.7%. The listed terms are not a complete account of every possible adverse event, and the registry record does not provide event-level detail in the registry record.

Deaths are not reported in the registry record. The duration of safety follow-up for each participant, event adjudication procedures, and statistical comparisons of serious adverse events are also not reported in the registry record. Interpretation should therefore remain limited to the posted counts and terms, without inferring causation or making a treatment-safety judgment from these summaries alone.

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

The primary result describes a Week 24 comparison of DAS28 remission under two strategies that both include tocilizumab: continuing methotrexate or using placebo in its place during the initial treatment period. The posted percentages are 40.4% and 34.8%, respectively. The sponsor’s reported primary analyses and the unadjusted recalculation both leave meaningful uncertainty around the comparison. The results do not establish a clear difference at that time point.

This conclusion is not the same as saying that the strategies are equivalent. Failure to rule out no difference does not prove that there is no difference. Equivalence or noninferiority requires a prespecified margin and an analysis designed to answer that question; such details are not reported in the registry record. Likewise, a result that is statistically uncertain does not establish that either strategy is better or worse in a clinical sense.

The endpoint is a threshold-based measure of disease activity. It captures whether a participant met the specified remission threshold at Week 24, but it does not summarize every dimension of rheumatoid arthritis, the full trajectory of scores, or outcomes that were not recorded. The later treatment-adjustment provisions also mean that the Week 24 comparison and outcomes after that point address different stages of the study.

The registry results apply to the trial’s recorded population and treatment strategies. The primary population is described as randomized participants who received study drug. The findings should not be assumed to apply unchanged to people with different treatment histories, disease characteristics, or care contexts. Details needed to assess those forms of generalizability are not reported in the registry record.

Finally, posted outcome percentages and statistical tests are evidence summaries, not individualized predictions. They do not determine what will happen for a particular person, and the registry record does not provide enough information to resolve every question about missing data, multiplicity, or the original statistical plan.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares two active strategies that share tocilizumab and differ in whether methotrexate is continued during the initial treatment period. That design makes the contrast specific: it concerns the added strategy of methotrexate alongside tocilizumab, rather than the effect of tocilizumab compared with no tocilizumab.

The primary endpoint is clinically interpretable as a remission threshold, yet the statistical comparison illustrates why observed percentages should not be read in isolation. The methotrexate arm has the higher posted Week 24 percentage, but the sponsor’s confidence intervals include the null value and the unadjusted risk-difference interval includes zero. The magnitude and precision of an estimate both matter when drawing conclusions.

The registry also shows why results across endpoints need careful organization. Continuous disease-activity summaries, later remission outcomes, and withdrawal events do not measure identical things. Some secondary analyses appear more statistically distinct than the primary Week 24 comparison, but multiple outcomes and time points complicate the weight that should be placed on any one secondary result.

Finally, a registry record can provide useful outcome and design information while leaving important analytic details unclear. Here, the recorded analysis population is specified, but missing-data handling, multiplicity procedures, and the original sample-size justification are not reported. Recognizing these boundaries is part of interpreting clinical-trial statistics responsibly.

19. Limitations

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

Several limitations are specific to interpreting this registry record. The primary analysis population is defined as randomized participants who received study drug rather than all randomized participants, and the record does not explain how many randomized participants did not meet that condition or why. The approach to missing Week 24 measurements is not reported, so the potential effect of missing outcomes cannot be assessed from these registry entries.

The primary outcome comparison has confidence intervals that include the null value. This limits the certainty with which the direction and size of a Week 24 difference can be described. The primary result should not be converted into a claim of equivalence or no effect, particularly because an equivalence or noninferiority margin and analysis are not reported.

The intervention descriptions are truncated after the text for later treatment adjustments begins. The brief summary states that changes in treatment intensity could occur after the initial 24-week blinded period, but the detailed adjustment rules and the extent to which participants received changes are not reported in the registry record. That limits interpretation of results after Week 24 as a simple continuation of the initial assigned regimens.

The record lists many outcomes and analyses, but the multiplicity plan and statistical analysis plan are not reported. Results for most listed secondary measures are also not reported in the registry record. The safety summary gives serious-event counts and selected terms, but deaths and additional event details are not reported in the registry record.

Finally, the registry records both a target sample size of approximately 470 and enrollment of 556, without explaining the difference or reporting the original sample-size rationale. The planning illustrations based on observed effects do not fill that gap and should not be mistaken for the trial’s original design assumptions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of Tocilizumab and Methotrexate Treatment Strategies (Adding Tocilizumab to Methotrexate Versus Switching to Tocilizumab) in Patients With Active Rheumatoid Arthritis With Inadequate Response to Prior Methotrexate Treatment — NCT00810199.
• Registry record last updated 2014-07-18; status last verified 2014-07.
• Results first posted 2014-07-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The record describes a completed Phase 3 randomized, parallel-group study in people with active rheumatoid arthritis and inadequate response to prior methotrexate. It compared tocilizumab with continued methotrexate against tocilizumab with placebo in place of methotrexate during the first 24 weeks. The primary outcome was DAS28 remission at Week 24.

The posted Week 24 remission percentages were 40.4% and 34.8%. The sponsor’s reported odds-ratio analyses had confidence intervals that included 1, while the unadjusted recalculation had a risk-difference interval that included zero. These results leave uncertainty about the primary comparison rather than establishing a clear difference.

Secondary outcomes provide additional, varied context. Important details about multiplicity, missing-data handling, the original sample-size justification, and several secondary results are not reported in the registry record.