A Study Comparing SB4 to Enbrel® in Subjects With Moderate to Severe Rheumatoid Arthritis Despite Methotrexate Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study Comparing SB4 to Enbrel® in Subjects With Moderate to Severe Rheumatoid Arthritis Despite Methotrexate Therapy (NCT01895309), a randomized phase 3 study. The primary outcome is American College of Rheumatology 20% Response Criteria (ACR20).

2. Clinical Question

3. Trial Design

The registry describes a Phase 3, randomized, double-blind, parallel-group, multicentre clinical study. It records quadruple masking. The study was designed to evaluate efficacy, safety, pharmacokinetics and immunogenicity of SB4 compared with Enbrel in participants with moderate to severe rheumatoid arthritis despite methotrexate therapy. The record names Samsung Bioepis Co., Ltd. as sponsor and lists the study status as completed.

The two treatment groups received weekly subcutaneous injections: SB4 50 mg/week or Enbrel 50 mg/week. The primary endpoint was the percentage of participants meeting ACR20 response criteria at Week 24. Secondary results include ACR20 at Week 52 and ACR50 at Week 24 and Week 52. The record also describes an open-label extension in some countries after 52 weeks of treatment, during which participants would receive SB4 for an additional 48 weeks. The posted results discussed in the efficacy outcomes are not a report of that extension.

The registry records enrollment of 596. Outcome-specific denominators are reported separately and vary across the posted results. The record does not explain those denominator differences. It also does not report the trial’s original sample-size assumptions, the planned statistical analysis methods, or the analysis populations for the posted endpoints. Therefore, the numerical comparisons below describe the posted results and should not be read as a complete account of the protocol’s analysis.

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:

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 American College of Rheumatology 20% Response Criteria (ACR20), measured over Week 24.

The primary endpoint is the percentage of participants meeting the American College of Rheumatology 20% Response Criteria (ACR20) at Week 24. In general, a binary response endpoint classifies each participant as either meeting or not meeting a stated response criterion, then reports the proportion who meet it. ACR20 therefore represents a threshold-based response measure rather than a direct measure of every aspect of disease status. The registry record does not give further detail about how the response criteria were operationalized for this study.

A response threshold can make results easier to interpret as the share of participants reaching a defined level of response. It also simplifies a complex clinical outcome into a yes-or-no classification, so it does not show how far participants who meet the threshold exceed it, or how close those who do not meet it may be. A percentage comparison can describe how often the criterion was met in each group, but it does not by itself describe the full range of individual outcomes.

Week 24 is the specified primary assessment time. The registry also posts later ACR20 results and ACR50 results as secondary outcomes. Those measures offer related but distinct views of response; they do not replace the prespecified primary endpoint. The record does not report the detailed rationale for choosing ACR20 or Week 24 as the primary endpoint.

7. Results Posted in the Registry

• Enbrel (Etanercept): 80.5% (190/236) versus 78.1% (193/247) on control; risk difference 2.4 percentage points (95% CI -4.8 to 9.6), risk ratio 1.03 (0.94–1.13); unadjusted two-proportion z-test p = 0.520.

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.

ACR20

• 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:
  • Enbrel (Etanercept): 81.5% (176/216) versus 80.8% (181/224) on control; risk difference 0.7 percentage points (95% CI -6.6 to 8.0), risk ratio 1.01 (0.92–1.10); unadjusted two-proportion z-test p = 0.856.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enbrel (Etanercept) and the control. The interval gives the range of effects that remain compatible with the data.

American College of Rheumatology 50% Response Criteria (ACR50)

• 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:
  • Enbrel (Etanercept) at Week 24: 42.4% (100/236) versus 46.2% (114/247) on control; risk difference -3.8 percentage points (95% CI -12.6 to 5.1), risk ratio 0.92 (0.75–1.12); unadjusted two-proportion z-test p = 0.403.
  • SB4 (Proposed Biosimilar to Etanercept) at Week 52: 58.5% (131/224) versus 46.2% (114/247) on control; risk difference 12.3 percentage points (95% CI 3.4 to 21.3), risk ratio 1.27 (1.06–1.51); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Enbrel (Etanercept) at Week 24 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for SB4 (Proposed Biosimilar to Etanercept) at Week 52 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broadly add information about response at a later time and about meeting a more demanding response threshold. The ACR20 results at Week 52 follow a similar between-group pattern to the primary ACR20 result at Week 24. The ACR50 comparisons are less uniform across assessment times: the Week 24 unadjusted comparison does not show a clear separation, while the Week 52 unadjusted contrast is more favorable to SB4. This overall pattern should be considered alongside, rather than instead of, the primary Week 24 result.

ACR20 and ACR50 are related response measures, but they are not interchangeable. ACR50 applies a different threshold than ACR20, so their response proportions and group contrasts need not match. Looking across both can describe whether the broad pattern is consistent across response definitions and time points. It cannot, by itself, establish a treatment effect across all outcomes, particularly when the registry record does not report a prespecified multiplicity plan or the methods used for the secondary analyses.

Unadjusted secondary results carry less confirmatory weight because the more outcomes and assessment times examined, the greater the chance of at least one apparently notable finding arising by chance. This is a general statistical concern, not a claim that any particular secondary result is false. A multiplicity strategy can account for that issue, but none is reported in the registry record. The record also lists no sponsor-reported analyses for these secondary outcomes. The posted comparisons therefore provide descriptive and exploratory context, rather than a substitute for a fully reported confirmatory analysis.

Differences in the reported denominators across the time points also limit simple interpretations of change over time. The registry does not state why those denominators differ or whether the same analysis population was used for each endpoint. The pattern across secondary outcomes is therefore best read as a set of separate posted comparisons, not as a complete account of within-participant change.

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

• ACR20
• American College of Rheumatology 50% Response Criteria (ACR50)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary: each participant either met the ACR20 response criterion at Week 24 or did not, and the reported outcome is the percentage meeting that criterion. The comparison can be expressed as a difference between two group proportions. A risk difference is an absolute contrast on the probability scale; its sign depends on which group is subtracted from which. In this comparison, the estimate of 0.024 is oriented toward Enbrel relative to SB4, as reflected by the reported group proportions. The interval from -0.049 to 0.096 includes zero, meaning that the data are compatible with no difference as well as with differences in either direction.

What does the confidence interval describe?

In general, a confidence interval describes the uncertainty around an estimated effect under the statistical method used. A narrower interval indicates more precision, while a wider interval leaves more uncertainty about the effect’s size and direction. It is not a range containing a fixed proportion of individual participant outcomes, and it does not give the probability that the true effect lies within the particular interval. The registry record does not identify the method used to create the posted interval, so its construction should not be inferred.

What does the p-value add?

The unadjusted p-value for the primary comparison is 0.52. In general, a p-value measures how incompatible the observed data are with a specified null hypothesis, conditional on the test’s assumptions. It does not measure the probability that the null hypothesis is true, nor does it quantify the clinical importance of an effect. The registry record does not report the planned statistical test or adjustment strategy. The p-value should therefore be understood as the posted unadjusted comparison, not assumed to be the trial’s full sponsor analysis.

Why distinguish absolute and relative measures?

The posted comparison includes absolute and relative effect measures. A risk difference describes an absolute separation between group response probabilities. A risk ratio compares those probabilities multiplicatively, and an odds ratio compares the odds of response. These measures answer different questions and can have different numerical values even when calculated from the same underlying outcomes. For the primary endpoint, the posted risk ratio is 1.03 with a confidence interval from 0.941 to 1.129, and the posted odds ratio is 1.156 with a confidence interval from 0.743 to 1.797. Both intervals include the respective null value of 1. In general, an interval for a ratio that includes 1 does not rule out no relative difference under that measure.

The posted group percentages are rounded, while the comparison statistics use the underlying counts and denominators recorded for the analysis. Small differences between a calculation based on displayed rounded percentages and a comparison based on counts can arise from rounding. The relevant posted values should be read as rounded summaries, not as exact individual-level data.

Why can binary outcomes be sensitive to analysis choices?

Binary response analyses depend on how participants are classified and on which participants are included at each assessment. Missing outcome values, treatment discontinuation, protocol deviations and the choice of analysis population can affect the estimate. These are general considerations for binary outcomes; the registry record does not report how missing responses were handled, whether any imputation was used, or which analysis population was used for the primary endpoint.

For a response proportion, the number of participants observed at the assessment affects precision. The denominators reported for Week 24 and Week 52 are not the same, and the record does not state why. This prevents a reader from attributing the denominator changes to a particular cause, such as withdrawal, missing assessment or a defined analysis rule. It also means that a comparison across time points is not necessarily a comparison of exactly the same participants.

Why do secondary comparisons need caution?

Testing several outcomes or assessment times increases the opportunity to observe a nominally small p-value by chance. In general, multiplicity procedures address this issue by controlling a chosen error rate across a family of comparisons. The registry record does not report a multiplicity adjustment or define a family of tests. The secondary p-values are therefore best interpreted as unadjusted comparisons rather than as definitive confirmatory evidence. The record lists no sponsor-reported analyses for the posted secondary results.

The registry also does not report the original statistical analysis plan, model specifications, stratification factors, covariate adjustments, interim analyses or a sample-size justification. Those details matter because they can affect both the estimate and its uncertainty. In their absence, the posted simple comparisons should not be mistaken for a complete reconstruction of the trial’s planned analysis. No discrepancy is flagged between the posted outcomes and the calculations used for these comparisons, but that does not fill in unreported protocol details.

11. Confidence Intervals and Precision

The Week 24 ACR20 risk-difference estimate is 0.024, with a confidence interval from -0.049 to 0.096. Because the interval includes zero, the posted results are compatible with no absolute difference as well as with an advantage in either direction. The interval’s breadth indicates that the estimate is not precise enough to pin down a narrow range of plausible group differences. The unadjusted p-value of 0.52 is consistent with that uncertainty; it is not evidence that the groups are exactly equal.

Precision is influenced by the amount of information available and by the variability inherent in the outcome. A binary endpoint has uncertainty because each participant contributes a response or nonresponse classification. In general, more informative observations can narrow uncertainty, while fewer usable observations or a less common event can make estimates less precise. The registry reports endpoint-specific denominators, but does not explain why they differ from the enrollment figure or between time points.

The ratio measures give another view of uncertainty. For the primary comparison, the risk ratio is 1.03 with a confidence interval from 0.941 to 1.129, and the odds ratio is 1.156 with a confidence interval from 0.743 to 1.797. Each interval includes 1, the null value for a ratio. These intervals likewise leave uncertainty about the direction and magnitude of a relative difference.

Confidence intervals describe statistical uncertainty under a method; they do not account automatically for every source of uncertainty, such as missing-data assumptions, unreported analysis choices or multiplicity. Those aspects are not detailed in the registry record. The limits should therefore be read alongside the design and reporting limitations, rather than as a complete measure of all uncertainty in the trial.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. 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 as the stated fraction of the observed effect. For these binary outcomes, the figures are participants per arm, not total events. The registry record does not report the original sample-size justification or the assumptions used when planning the trial.

The 80% power column describes the participant count per arm that the illustration estimates would give an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column makes the same kind of illustration for a 90% chance. These are design calculations for hypothetical future studies, not evidence about the probability that the completed trial detected an effect.

Rows using a smaller fraction of the observed effect represent a smaller target difference. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm under the stated assumptions. For example, the primary comparison’s illustration gives 4,580 participants per arm for 80% power when planning for 100% of the observed effect, and 18,706 participants per arm when planning for 50% of the observed effect. These values are illustrations, not recommended enrollment targets; their usefulness depends on whether the assumptions and target effect suit a future study.

This is not observed power. Observed power calculated from an estimated effect would not resolve the uncertainty in the completed trial’s confidence interval. The planning figures instead show how assumed effect size and desired power relate to a hypothetical sample size under the stated calculation 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 = 0.781; treatment proportion p₁ = 0.805; average p̄ = 0.793.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5727 = 1.1226.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5725 = 0.4818.
4. n = (1.1226 + 0.4818)² / (0.0237)² = 4,579.5, rounded up to 4,580 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 <- 0.781376518218624                          # control proportion
p1 <- 0.805084745762712                          # 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(1895309)
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 = 4,580 (80% power), 6,131 (90% power)
 75% of observed effect: n per arm = 8,229 (80% power), 11,015 (90% power)
 50% of observed effect: n per arm = 18,706 (80% power), 25,042 (90% power)
power.prop.test: 4579.5 
Simulated power at n = 4,580 per arm: 0.798 (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

The registry record does not report whether the trial used a multiplicity adjustment for the primary and secondary efficacy comparisons. It also does not define a family of hypotheses or state how statistical testing across outcomes and assessment times was controlled. This matters because repeated testing can increase the chance of at least one apparently significant result when no true effect exists. In general, a prespecified testing hierarchy or other adjustment can address that issue. Without the plan, the secondary p-values should be treated as unadjusted evidence.

The record lists no sponsor-reported analyses for the primary or secondary outcomes in the analysis fields. The posted comparison statistics are therefore not accompanied by a reported full analysis plan, model description or explanation of how the analyses were carried out. The original statistical methods, any interim analyses, and any adjustment for baseline variables or stratification are not reported in the registry record.

Missing-data handling is also not reported. The denominators differ between the primary Week 24 result and the later results. The registry does not say whether this reflects missing endpoint measurements, withdrawals, eligibility for a particular analysis population, or another reason. It does not state how participants with missing responses were classified or whether any imputation method was used. These omissions make it difficult to assess whether missing outcomes could affect the response estimates.

The registry does not identify the analysis population for each outcome, such as an intention-to-treat or per-protocol population. It would be inappropriate to infer one from the reported denominators alone. The record also does not give the original protocol’s analysis assumptions or enough information to reconstruct the sponsor’s planned inferential approach. These limitations do not invalidate the posted numbers, but they restrict how fully their statistical context can be assessed.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cellulitis (0.7%), neutropenia (0.3%), coronary artery disease (0.3%), chorioretinopathy (0.3%), enterocolitis (0.3%).

The registry reports serious adverse events for the SB4 group as 18 participants affected among 299 at risk, and for the Enbrel group as 15 affected among 297 at risk. These are counts with their reported at-risk denominators; they should be read as separate group summaries, not as proof that the treatments differ in safety. The record does not provide a comparative statistical analysis or confidence intervals for these figures.

Other adverse events are reported for 175 participants among 299 at risk in the SB4 group and 179 among 297 at risk in the Enbrel group. The registry lists cellulitis at 0.7% as a top serious adverse event term and neutropenia, coronary artery disease, chorioretinopathy, enterocolitis and gastritis at 0.3% each. Those listed terms do not constitute a complete account of all safety outcomes.

Deaths are not reported in the registry record. The safety figures alone do not establish whether an event was caused by treatment, and the posted record does not provide enough detail to characterize event timing, severity beyond the serious-event classification, or the full safety analysis.

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

The posted primary result describes ACR20 response proportions at Week 24 in the two randomized groups. The proportions are close in the displayed summaries, while the risk-difference confidence interval includes zero and spans possible differences in either direction. The unadjusted p-value does not provide strong evidence against a null difference, but neither it nor the interval demonstrates that the treatments are identical.

These results do not establish equivalence or noninferiority. Such conclusions require a suitable design and analysis, including a prespecified margin and methods appropriate to that objective. The registry record does not report a noninferiority margin or the trial’s planned analysis details. It is therefore not possible to infer those claims from the posted response percentages alone.

The results also do not answer every question about the treatments. The study assessed safety, pharmacokinetics and immunogenicity, but the efficacy results cannot stand in for those assessments. The safety summaries are counts without a reported comparative inferential analysis. The record does not report deaths. Nor do the posted endpoint percentages describe the full distribution of participant experiences or explain why outcome denominators differ.

Secondary outcomes provide context across another response threshold and a later assessment time, but they are not a replacement for the primary endpoint. Since multiplicity handling is not reported, unadjusted secondary results deserve cautious interpretation. A statistically notable secondary contrast does not by itself settle an overall efficacy question.

In general, a registry result is most informative when interpreted with the trial design, analysis plan, outcome definitions, missing-data methods and uncertainty estimates. Some of those details are not reported in the registry record. The defensible reading is therefore limited to the posted group summaries and comparisons, their stated precision, and the reporting gaps that constrain stronger conclusions.

17. Why This Trial Matters Statistically

This trial offers a randomized, masked, parallel-group comparison of a proposed etanercept biosimilar with Enbrel in participants with moderate to severe rheumatoid arthritis despite methotrexate therapy. That design makes a direct comparison possible, while the shared injection route and weekly dose provide a straightforward treatment contrast as described in the registry. The primary endpoint is a clearly named response measure assessed at a specified time point.

Statistically, the result is useful for illustrating why a point estimate, confidence interval and p-value need to be read together. The point estimate gives a direction and magnitude on the risk-difference scale; the interval shows substantial uncertainty around it; and the unadjusted p-value does not support a clear difference under the posted comparison. None of these alone establishes equivalence.

The record also illustrates the importance of distinguishing a primary result from secondary findings. A secondary comparison can look more compelling than the primary result, but its evidential weight depends on the planned testing strategy, which is not reported. Missing analysis details and unexplained denominator changes further limit interpretation. These are not merely reporting technicalities: they affect how confidently readers can connect observed response proportions to the study’s intended statistical question.

The planning illustrations provide a separate lesson. They show that a smaller target effect calls for a larger hypothetical sample under specified assumptions, but they are not a reconstruction of the trial’s original design and do not measure its observed power. Keeping such planning calculations distinct from the completed trial’s observed results helps prevent overinterpretation.

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.

Several trial-specific reporting gaps constrain interpretation beyond the uncertainty already reflected in the posted confidence intervals. The registry does not report the original sample-size justification, the protocol’s statistical analysis plan, the planned handling of missing outcomes, or the analysis populations used for the endpoints. It also does not state whether any interim analyses were conducted or whether the efficacy comparisons were adjusted for multiplicity.

The outcome denominators differ across the reported time points, but the record does not explain why. Without that information, changes in response summaries over time cannot confidently be attributed to within-participant change or to a particular pattern of missingness. The record does not describe imputation, treatment discontinuation handling or sensitivity analyses for missing data.

The comparison estimates posted in the registry are unadjusted, and the registry lists no sponsor-reported analyses for the efficacy outcomes. The record does not identify the statistical test or interval method used. Consequently, the displayed calculations should not be treated as a substitute for a full report of the trial’s planned analysis.

Safety reporting is also limited in the available record. Serious and other adverse-event counts are posted, but comparative uncertainty estimates and a full safety analysis are not. Deaths are not reported in the registry record. The listed serious adverse event terms are not a complete safety profile. These points limit the conclusions that can be drawn from the registry results alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study Comparing SB4 to Enbrel® in Subjects With Moderate to Severe Rheumatoid Arthritis Despite Methotrexate Therapy — NCT01895309.
• Registry record last updated 2017-08-17; status last verified 2015-12.
• Results first posted 2016-08-29.
• 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

The registry describes a completed Phase 3 randomized, double-blind, parallel-group, multicentre study of SB4 compared with Enbrel in moderate to severe rheumatoid arthritis despite methotrexate therapy. Both groups received 50 mg/week by subcutaneous injection. The primary outcome was ACR20 response at Week 24; later ACR20 and ACR50 outcomes were also posted.

At Week 24, the reported ACR20 proportions were 78.1% for SB4 and 80.5% for Enbrel. The unadjusted risk-difference estimate is 0.024, with a confidence interval from -0.049 to 0.096 and an unadjusted p-value of 0.52. The interval includes zero and leaves uncertainty about the direction and size of a difference. Multiplicity handling, missing-data methods, analysis populations and the original statistical plan are not reported in the registry record.