Study Evaluating Etanercept Plus Methotrexate in Early Rheumatoid Arthritis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study Evaluating Etanercept Plus Methotrexate in Early Rheumatoid Arthritis (NCT00913458), a randomized phase 4 study. The primary outcome is Number of Participants That Met Sustained Remission at Week 76 and Week 91 Based on DAS28 Score.

2. Clinical Question

The primary outcome is a count of participants meeting a multi-visit definition, rather than a single measurement of disease activity at one time. The question therefore concerns whether the remission threshold was met at both specified visits under the registry’s additional rule about corticosteroid boosts. The result is specific to the analyzed population and the recorded definition; it does not by itself describe every participant enrolled in the overall study.

The registry record gives an overall enrollment of 306, while the primary endpoint results are posted for Phase 2 groups. The endpoint population is further restricted by treatment exposure and availability of a post-randomization DAS28 evaluation. Details on how participants outside that analysis population were handled are not reported in the registry record.

3. Trial Design

The registry identifies this as a Phase 4, randomized, quadruple-masked, parallel study. Its title describes a three-phase study evaluating sustained remission and productivity outcomes among people with early rheumatoid arthritis initiated on etanercept plus methotrexate. The listed intervention is etanercept, and the arm description refers to etanercept plus methotrexate. The overall registry enrollment is 306.

The primary endpoint results are displayed for E25 + MTX (Phase 2), MTX + PBO (Phase 2), and Placebo (PBO) (Phase 2). These labels matter: the registry record also includes Phase 1 and Phase 3 group labels in its safety data, so the overall study enrollment and the primary endpoint group results should not be treated as the same analysis set. The record does not explain in detail how the phases connect, how participants moved between them, or whether all phases used identical procedures.

The primary analysis population is called modified intent-to-treat. It includes participants who received at least 1 dose of double-blind investigational product and had at least 1 post-randomization DAS28 evaluation. This is not the same as an analysis of every person enrolled, and the registry’s definition does not state how missing endpoint observations were treated.

Randomization and quadruple masking are reported, but the randomization method, allocation concealment procedures, identities of the masked groups, and details of treatment adherence are not reported in the registry record. The original sample-size justification, trial-specific power assumptions, interim analyses, and full statistical analysis plan are also not reported. The registry lists primary completion in 2012-06 and study start in 2009-09; the study status is completed.

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: Phase 1 responders, defined as subjects with Disease Activity Score based on 28-joints count (DAS28) ≤ 3.2 at Week 39 and DAS28 \<2.6 at Week 52, were randomized to Phase 2. The responders of Phase 2 were observed for 26-weeks in Phase 3 study that include 2 to 4 week period of double blind treatment taper of MTX followed by observational period

Only the first 6 of 7 groups are shown.

Phase 1

Reasons for not completing this period:

Phase 2

Reasons for not completing this period:

Phase 3

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified intent-to-treat (mITT) population, which included all participants who had taken at least 1 dose of double-blind investigational product and had at least 1 post-randomization DAS28 evaluation.

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: A total of 306 participants were enrolled in the study (Phase 1). Out of the 306 participants, 193 were eligible and were randomized at a ratio of 1:1:1 to Phase 2 study. Of the 193 participants from Phase 2, a total of 131 participants were eligible and were randomized to Phase 3 study.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants That Met Sustained Remission at Week 76 and Week 91 Based on DAS28 Score, measured over 76 and 91 weeks.

The primary endpoint counts participants who met sustained remission at Week 76 and Week 91 based on DAS28. The registry defines sustained remission as DAS28 <2.6 at both visits. It adds a corticosteroid-boost condition covering the interval between Week 52 and Week 64: a boost was defined as DAS28 >3.2 at either the Week 56 or Week 64 visit. The endpoint description says participants meeting sustained remission at both Week 76 and Week 91 are presented.

DAS28 uses the count of swollen joints and painful joints among 28 joints, erythrocyte sedimentation rate, and the patient’s global assessment of disease activity. Combining these components gives a structured measure of disease activity rather than relying on a single symptom or laboratory value. Applying the threshold at two later visits makes the endpoint about sustained status across those assessments, not merely a favorable value at one visit.

A binary endpoint is useful for communicating how many participants meet a prespecified clinical definition. It also makes group comparisons straightforward to express as differences in the proportion meeting that definition. However, reducing a continuous disease-activity measure to a yes-or-no outcome loses information about how far an individual’s score lies from the threshold. The registry record does not report additional details about the clinical rationale for the chosen threshold or the boost rule.

7. Results Posted in the Registry

• E25 + MTX (Phase 2): 63.5% (40/63) versus 23.1% (15/65) on control; risk difference 40.4 percentage points (95% CI 24.7 to 56.1), risk ratio 2.75 (1.70–4.45); unadjusted two-proportion z-test p = <0.001.
• MTX + PBO (Phase 2): 40.0% (26/65) versus 23.1% (15/65) on control; risk difference 16.9 percentage points (95% CI 1.2 to 32.6), risk ratio 1.73 (1.02–2.96); unadjusted two-proportion z-test p = 0.038.

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.

Number of Participants Achieving Complete Response (Using Disease Activity Score Based on a 28-joint Count, Modified Total Sharp Score, Health Assessment Questionnaire)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • E25 + MTX (Phase 2): 57.1% (36/63) versus 10.8% (7/65) on control; risk difference 46.4 percentage points (95% CI 32.0 to 60.7), risk ratio 5.31 (2.55–11.03); unadjusted two-proportion z-test p = <0.001.
  • MTX + PBO (Phase 2): 29.2% (19/65) versus 10.8% (7/65) on control; risk difference 18.5 percentage points (95% CI 5.1 to 31.8), risk ratio 2.71 (1.23–6.01); unadjusted two-proportion z-test p = 0.009.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for E25 + MTX (Phase 2) 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 MTX + PBO (Phase 2) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Modified Total Sharp Score (mTSS) at Week 52

• 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:
  • E25 + MTX (Phase 2): mean 8.40 versus 8.60 on control; difference -0.20 (95% CI -5.19 to 4.79), standardized effect d = -0.02; z-test p = 0.937.
  • MTX + PBO (Phase 2): mean 8.40 versus 8.60 on control; difference -0.20 (95% CI -5.54 to 5.14), standardized effect d = -0.01; z-test p = 0.941.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between E25 + MTX (Phase 2) 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 MTX + PBO (Phase 2) and the control. The interval gives the range of effects that remain compatible with the data.

Work Productivity and Activity Impairment (WPAI) Questionnaire: Percent Work Time Missed in the Past 7 Days Due to Problem

• 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:
  • E25 + MTX (Phase 2): mean 0.20 versus 0.00 on control; difference 0.20 (95% CI -0.24 to 0.64), standardized effect d = 0.23; z-test p = 0.369.
  • MTX + PBO (Phase 2): mean 0.10 versus 0.00 on control; difference 0.10 (95% CI -0.08 to 0.28), standardized effect d = 0.21; z-test p = 0.274.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between E25 + MTX (Phase 2) 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 MTX + PBO (Phase 2) and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary outcomes, including complete response, structural change measured by modified Total Sharp Score, work productivity and activity impairment, and ACR response measures. The posted secondary results therefore span binary response outcomes, a continuous structural measure, and patient-reported productivity measures. This breadth adds context around the primary sustained-remission endpoint but does not make those outcomes interchangeable with it.

The overall pattern should be interpreted outcome by outcome, in light of each measure’s definition, analysis population, timing, and uncertainty. Some secondary measures address related aspects of disease activity or response, while productivity measures address different consequences and should not be treated as direct replications of the remission result. The registry reports 37 secondary outcomes as posted and lists 38 outcome measures overall, with 72 analyses. Those counts indicate that many statistical comparisons may be involved.

The selected secondary results include comparisons with different observed patterns and levels of precision; they should be considered alongside their intervals and analysis methods rather than condensed into a single claim that all outcomes agree. The continuous outcomes are especially distinct in scale and interpretation from the binary primary endpoint. No sponsor-reported analysis is listed for the posted modified Total Sharp Score and WPAI examples described in the record.

Unadjusted secondary p-values carry less weight when many outcomes and comparisons are examined because the chance of at least one apparently notable result can increase across a collection of tests. Whether a multiplicity adjustment was planned or applied is not reported in the registry record. Accordingly, secondary findings are most useful as supportive or exploratory context unless a prespecified hierarchy and analysis procedure can be established. They do not independently confirm the primary result merely because their direction or statistical significance appears favorable.

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

• Number of Participants Achieving Complete Response (Using Disease Activity Score Based on 28-joint Count, Modified Total Sharp Score, Health Assessment Questionnaire)
• Change From Baseline in Modified Total Sharp Score (mTSS) at Week 52 and Final on Therapy
• Change From Baseline in Work Productivity and Activity Impairment (WPAI) Questionnaire: Percent Overall Work Impairment Due to Problem
• Change From Baseline in Work Productivity and Activity Impairment (WPAI) Questionnaire: Percent Impairment While Working Due to Problem
• Change From Baseline in Work Productivity and Activity Impairment (WPAI) Questionnaire: Percent Work Time Missed Due to Problem
• Change From Baseline in Work Productivity and Activity Impairment (WPAI) Questionnaire: Percent Activity Impairment Due to Problem
• Number of Participants Achieving American College of Rhematology 20% (ACR 20) Response
• Number of Participants Achieving American College of Rhematology 50% (ACR 50) Response

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary endpoint is binary: each participant either met the sustained-remission definition or did not. A comparison of binary outcomes can be expressed in several ways. The registry’s reported analyses use logistic regression and present odds ratios, while the recalculations use unadjusted risk differences from the posted counts. These measures answer related but different questions, so their numerical values are not interchangeable.

What an odds ratio describes

An odds ratio compares the odds of meeting the endpoint between groups. Odds are not the same as probabilities: probability is the fraction meeting the endpoint out of the group, whereas odds compare those meeting it with those not meeting it. An odds ratio above 1 indicates higher estimated odds in the first named group relative to the comparison group, given the direction of that comparison. It does not mean that the probability is multiplied by the odds ratio.

Logistic regression is a standard method for modeling a binary outcome. The registry reports the method and the odds ratio, but the model’s covariates, any stratification factors, and the handling of missing observations are not reported in the registry record. Therefore, the reported odds ratio should be understood as the sponsor’s posted analysis estimate, without assuming additional adjustment details.

What the unadjusted recalculation describes

The recalculated risk difference is a direct contrast between the observed group proportions, based on the posted event counts and denominators. It is unadjusted: it does not account for participant characteristics or other model terms. A confidence interval around a risk difference gives a range of values compatible with the observed data under the calculation’s assumptions. A p-value addresses how unusual data at least as discrepant as those observed would be under a specified null model; it does not measure the probability that a hypothesis is true.

For the primary comparison, the recalculated unadjusted p-value is <0.001; for MTX + PBO versus placebo, it is 0.038. The sponsor-reported analyses use logistic regression and include confidence intervals and p-values. Differences between an unadjusted recalculation and a model-based result can arise because the methods and estimands differ. They should not be treated as competing versions of the same calculation without knowing the full model specification.

Why confidence intervals matter

A confidence interval communicates the precision of an estimated effect under the method used. A relatively narrow interval indicates less statistical uncertainty than a wider interval, though it does not account for every possible source of bias or uncertainty. If an interval for a difference includes zero, the data are compatible with no difference at the confidence level used, as well as with values on either side of zero. For an odds ratio, the corresponding null value is 1. These are general interpretations of the measures; they do not substitute for the trial’s full analysis plan.

Planning illustrations

The sample-size illustrations use the observed effect or a stated fraction of it, a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They show participants per arm for the binary comparisons. Smaller effects require more participants under these assumptions because a smaller signal is harder to distinguish from random variation. These calculations are planning illustrations, not the trial’s original design calculation. The original design assumptions are not reported in the registry record.

For safety summaries and continuous secondary outcomes, the statistical interpretation depends on the outcome scale and available observations. A count of participants with an event is not equivalent to a continuous mean, and a mean difference should be read together with its dispersion and interval. The registry lists standard deviations for the posted continuous outcomes, but no sponsor-reported analyses for those selected outcomes. The recalculated comparisons are unadjusted and should not be mistaken for the full trial analysis.

11. Confidence Intervals and Precision

For the primary comparison of E25 + MTX with placebo, the sponsor-reported odds ratio is 5.8 and its 95% confidence interval runs from 2.7 to 12.5. This interval is on the odds-ratio scale: it describes uncertainty in the estimated relative odds, not a range of participant counts or a direct range for the absolute difference between groups. The interval lies above the odds-ratio null value of 1, consistent with the reported p < 0.001 under that analysis.

The sponsor-reported odds ratio for MTX + PBO versus placebo is 2.22, with a 95% confidence interval from 1.0 to 4.8. The lower endpoint is at the null value as displayed after rounding, and the reported p-value is 0.040. Rounding means the displayed interval endpoints and p-value need not appear to give an exact boundary judgment when read in isolation. The registry’s displayed precision should be preserved rather than treated as more exact than it is.

A confidence interval is a measure of sampling uncertainty under the analysis model. It is not a guarantee that the true value lies within the particular displayed interval, and it does not incorporate every potential problem in study conduct, outcome measurement, selection, or missing data. The posted intervals are for the reported comparisons; the registry record does not provide a complete account of any multiplicity adjustment.

The observed counts also help convey precision: the primary groups include 63, 65, and 65 participants, respectively. Those group sizes describe the posted endpoint analysis, not the full enrollment. When event counts and analysis groups are limited, estimates can be sensitive to a small number of outcomes. The interval is therefore important alongside the point estimate, and neither alone captures all uncertainty about how the result might generalize.

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 display gives planning illustrations for the binary comparisons in participants per arm, not total events. It uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The detectable effect is set in turn to the observed effect, 75% of the observed effect, or 50% of the observed effect. The trial’s original design assumptions are not reported in the registry record.

The 80% power column gives the illustrative participants per arm for a design that would have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and model assumptions held. The 90% power column gives the corresponding planning figure for a higher chance of detection. These are design calculations, not descriptions of what happened in the completed study. For example, the E25 + MTX versus placebo illustration lists 23 participants per arm for 80% power when planning for 100% of the observed effect, and 85 per arm when planning for 50% of that effect. The larger requirement for the smaller target effect illustrates the general relationship: smaller effects need more participants to detect reliably.

Values can become very large when the observed continuous-outcome difference is small relative to variability; such values are mathematical consequences of the stated planning setup, not suggested enrollment targets for the original study. The figures are not observed power, and they should not be used to infer the study’s original sample-size justification or the probability that its findings are correct.

The curve should be read as another view of how a planning quantity changes across assumed effects, under its stated calculation. It does not add trial observations or replace the confidence intervals around the posted results. Planning from an observed effect can be optimistic, especially when the observed estimate is unstable, so the illustrations are most useful for understanding sensitivity to the assumed effect size rather than as definitive design recommendations.

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 = 0.231; treatment proportion p₁ = 0.635; average p̄ = 0.433.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7007 = 1.3733.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6398 = 0.5384.
4. n = (1.3733 + 0.5384)² / (0.4042)² = 22.4, rounded up to 23 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 <- 0.230769230769231                          # control proportion
p1 <- 0.634920634920635                          # 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(913458)
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 = 23 (80% power), 30 (90% power)
 75% of observed effect: n per arm = 40 (80% power), 52 (90% power)
 50% of observed effect: n per arm = 85 (80% power), 113 (90% power)
power.prop.test: 22.4 
Simulated power at n = 23 per arm: 0.820 (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 sponsor’s posted primary analysis uses logistic regression and reports odds ratios with 95% confidence intervals and p-values. For E25 + MTX versus placebo, the reported odds ratio is 5.8 (95% confidence interval 2.7 to 12.5; p < 0.001). For MTX + PBO versus placebo, the reported odds ratio is 2.22 (95% confidence interval 1.0 to 4.8; p = 0.040). These estimates are broadly consistent in direction with the posted counts and the unadjusted recalculations.

The recalculations are simple, unadjusted comparisons of the registry’s summary counts. They do not reproduce logistic regression or any possible model adjustments. The sponsor also reports an E25 + MTX versus MTX + PBO odds ratio of 2.61, with a 95% confidence interval of 1.3 to 5.3 and p = 0.009; that is a different pairwise contrast from the two placebo comparisons emphasized in the recalculations.

Where the sponsor analysis and simple recalculation differ, the sponsor’s own analysis is the primary reported analysis. The registry record does not provide enough model detail to explain every numerical difference. The recalculations are best treated as transparent checks based on posted summaries, not as replacements for the sponsor’s regression analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports 38 outcome measures, 72 analyses, and 37 posted secondary outcomes. This indicates a substantial collection of endpoints and comparisons. When many hypotheses are tested, the chance of obtaining at least one small p-value by chance increases. Common approaches to address this include controlling a family-wise error rate, controlling a false-discovery rate, or using a prespecified testing hierarchy. These are general methods; which, if any, were used in this study is not reported in the registry record.

The primary endpoint is identified, but the record does not provide a full multiplicity plan describing how it related to the other outcomes or comparisons. The sponsor-reported p-values and the unadjusted recalculated p-values should therefore be read as reported for their particular comparisons, not assumed to account for all analyses in the study. This does not invalidate the estimates, but it affects how strongly individual secondary p-values support confirmatory conclusions.

The primary modified intent-to-treat definition requires at least 1 dose of double-blind investigational product and at least 1 post-randomization DAS28 evaluation. The registry does not report the number of participants excluded from this population, the amount or pattern of missing endpoint data, reasons for missingness, or the method used to handle missing values. It also does not report whether sensitivity analyses assessed alternative missing-data assumptions.

These omissions matter because an endpoint measured at later visits may be unavailable for some participants, and the interpretation of a binary outcome can depend on how absent assessments are handled. The posted group counts remain informative as the recorded results, but without fuller missing-data details the potential impact of incomplete follow-up cannot be assessed from the registry record alone. The original statistical analysis plan and trial-specific sample-size justification are also not reported, limiting assessment of prespecification and planned error control.

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: oral infection (3.1%), vasculitis (3.1%), pericarditis (1.6%), ear canal stenosis postoperative (1.6%), bacterial pyelonephritis (1.6%).

The safety summary lists serious adverse events and other adverse events separately, with affected participants and participants at risk reported by phase-labeled group. For example, the Phase 1 ETN 50 QW + MTX group lists 28 participants with serious adverse events and 130 with other adverse events among 306 at risk for each category. The Phase 2 and Phase 3 entries have their own denominators and should be read within their respective group labels rather than combined.

The listed serious-event terms include oral infection and vasculitis at 3.1% each, followed by pericarditis, ear canal stenosis postoperative, bacterial pyelonephritis, and cystocele at 1.6% each. These are registry-listed terms and percentages; the record excerpt does not provide further context about their timing, severity beyond the serious-event classification, or causal attribution.

Counts of participants with events do not describe the total number of event episodes, and they do not by themselves establish that treatment caused an event. The registry’s deaths fields are not populated in these safety summaries, so deaths are not reported in the registry record. Differences between phase groups cannot be interpreted as direct randomized safety contrasts without additional information about their design and follow-up.

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

The primary result describes how many participants in the posted analysis groups met a particular sustained-remission definition at Week 76 and Week 91. The observed counts were higher in the E25 + MTX group than in the posted placebo group and the MTX + PBO group. The sponsor’s logistic-regression comparison with placebo reports an odds ratio above 1, with a confidence interval above the odds-ratio null value as displayed. These are statistical descriptions of the recorded outcomes.

The result does not mean that every participant in a group had the same outcome, nor does an odds ratio translate directly into an individual probability. It does not establish a participant’s future outcome or address treatment choices. The primary endpoint is a specific threshold-based measure requiring results at two visits and applying a corticosteroid-boost rule; other definitions or time points could yield different summaries.

The registry record does not establish that every possible source of bias or uncertainty has been addressed. The endpoint analysis population is modified intent-to-treat, and details about missing observations, covariate adjustment, multiplicity, and the original design assumptions are not reported. The overall enrollment figure should not be confused with the endpoint analysis group sizes.

Secondary endpoints can broaden the description of disease response, structural outcomes, and productivity, but they are not substitutes for the primary endpoint. Their interpretation depends on their own definitions and analyses, and the number of outcomes makes multiplicity relevant. Safety counts also require caution: they describe recorded events by group and phase but do not, by themselves, establish causality or permit simple comparisons across phases.

In short, the posted results support a statistical contrast in the observed sustained-remission outcome for the analyzed groups. The strength and scope of any broader conclusion depend on the analysis details and limitations that are not fully documented in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definitions are central to statistical interpretation. Sustained remission is not simply a single low DAS28 measurement: the registry requires the threshold at Week 76 and Week 91 and includes a rule about corticosteroid boosts during an earlier interval. That definition determines which participants count as having the event, and therefore shapes every group comparison.

It also demonstrates the difference between an observed group contrast and a model-based estimate. The posted counts allow an unadjusted comparison, while the sponsor reports logistic-regression odds ratios. Both can be informative, but they express effects on different scales and may depend on different assumptions. A clear statistical reading keeps the estimand, analysis population, and method in view instead of treating all estimates as interchangeable.

The study’s multi-phase record highlights another practical issue: overall enrollment, phase-specific groups, safety populations, and endpoint populations may not align. Readers need to distinguish those populations rather than assume that a single enrollment number describes every analysis. The registry’s modified intent-to-treat definition makes this especially important.

Finally, the record lists many outcomes and analyses, alongside secondary measures covering disease activity, structural change, and productivity. This makes multiplicity and prespecification important to interpretation. Confidence intervals, missing-data details, and the sponsor’s full analysis plan would help assess precision and robustness, but some of those details are not reported. These are general statistical lessons illustrated by this record, not claims about clinical care.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record leaves important design and analysis details unspecified. It reports randomization and quadruple masking but does not describe sequence generation, allocation concealment, who was masked, or how masking was maintained. It also does not give the original sample-size justification, trial-specific power assumptions, interim-analysis plan, or full statistical analysis plan.

The primary endpoint population is modified intent-to-treat rather than all enrolled participants. The record does not state how many people lacked a post-randomization DAS28 assessment, how missing visits were handled, or whether sensitivity analyses were performed. Because the endpoint relies on assessments at Week 76 and Week 91 and a rule involving earlier visits, incomplete follow-up could affect who is classed as meeting the endpoint; its impact cannot be assessed from the posted description.

The overall study is described as three-phase, while the primary outcome results are labeled Phase 2 and the safety summary includes Phase 1, Phase 2, and Phase 3 groups. The registry record does not fully explain the relationship among these phases or how participants entered the endpoint analysis. Thus, overall enrollment should not be used as a substitute for the specific analysis denominators.

The record lists many outcome measures and analyses, but a multiplicity strategy is not reported. Secondary p-values may therefore be less persuasive as confirmatory evidence. The selected continuous secondary results have no sponsor-reported analyses listed, and their unadjusted recalculations cannot supply the missing model or study-plan details. Safety listings also lack enough contextual information to establish causality or support simple comparisons across phase groups.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study Evaluating Etanercept Plus Methotrexate in Early Rheumatoid Arthritis — NCT00913458.
• Registry record last updated 2014-07-17; status last verified 2014-07.
• Results first posted 2014-07-17.
• 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 registry record describes a completed Phase 4 randomized, quadruple-masked, parallel study of etanercept plus methotrexate in early rheumatoid arthritis, with overall enrollment of 306. The primary outcome is the number of participants meeting sustained remission at Week 76 and Week 91, defined using DAS28 thresholds and a corticosteroid-boost rule.

Primary results are posted for E25 + MTX, MTX + PBO, and placebo Phase 2 groups within a modified intent-to-treat population. The observed sustained-remission count is higher in the E25 + MTX group than in the posted comparator groups. Sponsor-reported logistic analyses and simple unadjusted recalculations offer related but methodologically distinct comparisons.

The registry also reports secondary outcomes spanning response, structural change, and productivity, along with phase-labeled adverse-event summaries. Details on multiplicity, missing-data handling, and the original design assumptions are not reported in the registry record, so these results are best interpreted within the limits of the recorded populations and methods.