Treatment of Early Aggressive Rheumatoid Arthritis (TEAR): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Treatment of Early Aggressive Rheumatoid Arthritis (TEAR) (NCT00259610), a randomized phase 4 study. The primary outcome is Disease Activity Score Erythrocyte Sedimentation Rate(DAS28-ESR).

2. Clinical Question

The registry identifies a randomized, factorial trial of treatments for early aggressive rheumatoid arthritis. Its primary outcome is a continuous disease activity score, so the posted group summaries describe averages and their variability rather than the proportion of participants who crossed a response threshold. The comparison summaries use the immediate methotrexate-plus-etanercept group as the reference. They do not, by themselves, report a single overall factorial effect or a formal test of whether treatment strategy and combination interact.

The trial description includes both a choice of combination therapy and a choice between immediate and step-up treatment. Those questions are related but not identical: the group summaries compare particular combinations of timing and drug regimen. Any broader conclusion about the two factors separately would require an analysis that accounts for the factorial structure. Such an analysis is not reported in the registry record.

3. Trial Design

The Treatment of Early Aggressive Rheumatoid Arthritis trial, also identified as TEAR, is listed as a phase 4 randomized factorial study. Its status is completed. The registry lists University of Alabama at Birmingham as the sponsor and records enrollment of 755. The recorded study start is 2004-05 and primary completion is 2009-06.

The four arm descriptions combine methotrexate with either etanercept or sulfasalazine and hydroxychloroquine, and distinguish immediate combination treatment from a step-up strategy. In the immediate groups, the combination drugs were started with methotrexate. In the step-up groups, the description identifies methotrexate alone or methotrexate with the relevant combination. The registry lists methotrexate, sulfasalazine, hydroxychloroquine, and etanercept as drug interventions.

Masking is recorded as quadruple. The registry record does not explain which people were masked or how masking was maintained. It also does not report the randomization procedure, allocation concealment, the factorial analysis plan, or details of how participants moved between treatment stages. Those design details should not be inferred from the arm labels.

The primary outcome population is described as randomized participants who completed the study to year 2. Group-specific analysis counts are reported alongside the primary outcome, but the record does not explain in detail how missing observations or participants who did not complete follow-up were handled. Enrollment is not interchangeable with the analysis counts for a particular outcome. The trial's original sample-size assumptions and justification 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.

Before assignment: This study had a screening period of 1-3 days, Patients were excluded for various reasons, including, laboratory exclusions, Positive TB test, and Cataract/visual defect.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The participants that were randomized into this clinical trial and completed the study to year 2, represent the number for analysis.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Disease Activity Score Erythrocyte Sedimentation Rate(DAS28-ESR), measured over Change of the Mean of DAS28-ESR between weeks 48 - 102..

The primary endpoint is the change in mean Disease Activity Score using 28 joints and erythrocyte sedimentation rate, or DAS28-ESR, between weeks 48 and 102. It is a continuous score intended to represent current rheumatoid arthritis disease activity. The calculation combines tender and swollen joint counts, ESR, and a general health component. The joint counts include up to 28 joints.

The registry describes a DAS28-ESR range from 0.0 to 9.2. It states that a score above 5.1 means high disease activity and a score below 3.2 indicates low disease activity. The posted outcome is a mean score change across a specified interval; it is not a count of participants reaching either of those thresholds. Although the endpoint description identifies change over time, the posted group values are presented as observed-group means, with standard deviations, and the comparison summaries are framed as mean differences. The record does not clarify whether the reported means are change scores or endpoint values in a way that resolves this distinction beyond the stated timeframe and description.

As a general statistical explanation, continuous measures can retain information about the degree of a participant's score rather than reducing it to a yes-or-no category. A group mean gives a central summary, while the standard deviation describes variation among observations. This can help characterize the distribution of disease activity, but the mean alone does not show how many participants improved, worsened, or crossed a clinical threshold. The registry does not report a threshold-based primary endpoint.

7. Results Posted in the Registry

• MTX+ Immediate SSZ +HCQ: mean 2.90 versus 3.00 on control; difference -0.10 (95% CI -0.50 to 0.30), standardized effect d = -0.07; z-test p = 0.625.
• MTX + Step-up Etanercept: mean 3.10 versus 3.00 on control; difference 0.10 (95% CI -0.20 to 0.40), standardized effect d = 0.07; z-test p = 0.520.
• MTX + Step-up SSZ + HCQ(ST): mean 2.80 versus 3.00 on control; difference -0.20 (95% CI -0.57 to 0.17), standardized effect d = -0.15; z-test p = 0.284.

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.

Radiographic Disease Progression Between Baseline and Week 102 as Assessed by Van Der Heijde Modified Sharp Scores.

• 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:
  • MTX+ Immediate SSZ +HCQ: mean 7.30 versus 7.00 on control; difference 0.30 (95% CI -3.65 to 4.25), standardized effect d = 0.02; z-test p = 0.882.
  • MTX + Step-up Etanercept: mean 4.80 versus 7.00 on control; difference -2.20 (95% CI -5.00 to 0.60), standardized effect d = -0.17; z-test p = 0.124.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between MTX+ Immediate SSZ +HCQ 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 + Step-up Etanercept and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcome is radiographic disease progression between baseline and week 102, assessed by Van Der Heijde Modified Sharp Scores. It complements the primary disease activity score by representing a different dimension of rheumatoid arthritis: observed radiographic change rather than the DAS28-ESR measure. The registry provides group means and standard deviations for this outcome and comparison summaries for some contrasts, but lists no reported analyses.

Across the posted secondary comparison summaries, the confidence intervals include zero. The estimates are therefore uncertain in direction, and the outcome does not provide a clear inferential contrast that resolves the uncertainty in the primary result. This broad pattern should not be taken to mean that the two endpoints are interchangeable or that one validates the other. They capture different outcomes, and concordance or discordance would require interpretation in light of their measurement properties and analysis plans.

The secondary result carries less weight than a prespecified primary result for formal claims. General statistical explanation: testing multiple outcomes or many contrasts raises the chance that at least one result will appear notable by chance if the tests are considered without adjustment. The registry does not report a multiplicity strategy, a hierarchy of secondary hypotheses, or adjustment for the comparisons. The secondary endpoint should therefore be considered supportive and exploratory in the context of the posted record, not as an independent confirmatory finding.

The record does not report a comprehensive analysis of every factorial contrast for radiographic progression. The available pairwise summaries do not establish separate effects of combination choice and treatment timing. Nor does the record explain missing-data handling for the secondary endpoint or whether the radiographic outcome was analyzed in the same population as the primary outcome. Those omissions limit how directly it can be compared with the primary result.

The appropriate overall reading is that the primary and secondary summaries do not show a clearly separated pairwise signal in the posted intervals, while both retain uncertainty. This is not proof of no difference on either measure. Stronger conclusions would require the prespecified analysis plan, detail on missing observations, and multiplicity-aware analyses, none of which are reported in the registry record.

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

• Radiographic Disease Progression Between Baseline and Week 102 as Assessed by Van Der Heijde Modified Sharp Scores.

9. Statistical Interpretation

10. Statistical Methods Explained

What do the group summaries describe?

The primary endpoint is identified as a mean of a continuous measure, with standard deviation as its dispersion summary. The mean is the arithmetic average of the observed scores in the analyzed group. It gives a compact description of the group's central score, but it does not show the full distribution, whether observations cluster in subgroups, or how individual participants changed over time.

The standard deviation describes how spread out individual observations are around the group mean. A larger standard deviation means greater variability among observed scores; it is not the uncertainty around the estimated mean. The registry reports means and standard deviations for the four treatment groups, along with group-specific analysis counts. The primary population description says that the analyzed participants were randomized and completed the study to year 2. Details on exclusions, missing values, or the handling of incomplete follow-up are not reported in the registry record.

How should a mean difference be read?

A mean difference compares the mean in one group with the mean in the reference group. A negative estimate means the comparison group's posted mean is lower than the reference mean under the registry's reported subtraction direction; a positive estimate means it is higher. For a disease activity score, the numeric direction alone does not establish the clinical importance of a difference. The registry does not give a minimum clinically important difference for the endpoint.

The posted comparisons use methotrexate plus immediate etanercept as the reference. They are pairwise contrasts, not a single test of all treatment groups and not, by themselves, estimates of the independent effects of treatment timing and combination choice. In factorial designs, an analysis can assess main effects and whether the effect of one factor depends on the other. Such results are not reported in the registry record.

What does a confidence interval convey?

General explanation: a confidence interval expresses uncertainty around an estimate using a method intended to produce intervals with a stated long-run coverage property under its assumptions. A narrower interval indicates greater precision for the estimate than a wider interval. If an interval for a mean difference includes zero, the posted data do not rule out zero difference at that interval's confidence level. It also does not rule out every nonzero difference in the interval. The confidence level and construction method for these intervals are not reported in the registry record.

The intervals accompany the mean differences and should be interpreted together with the estimates. They show that the direction and magnitude of plausible differences are uncertain, rather than indicating that the true difference is exactly zero. The registry does not report adjustment for the several comparisons, so the intervals and p-values should be understood as unadjusted summaries rather than multiplicity-controlled evidence.

What does a p-value mean in this setting?

General explanation: a p-value describes how unusual data at least as discordant with a specified null model would be if that model and the analysis assumptions held. It is not the probability that the null hypothesis is true, nor the probability that the finding occurred by chance. A p-value does not measure the size or clinical importance of an effect. The posted p-values are labeled unadjusted, so they do not account for a family of comparisons in the registry summaries.

The registry record does not state the inferential model used for the primary comparisons, whether covariates were included, or how the factorial design informed those tests. Therefore, interpretation should remain tied to the observed group summaries and the posted unadjusted pairwise contrasts. The record does not identify a prespecified primary contrast among the three reported comparisons or report a global test across treatment groups.

Why can variability and analysis choices matter?

General explanation: greater variability makes it harder to estimate a group mean or distinguish mean differences with the same amount of information. Unequal analysis counts can also affect precision across comparisons. If a continuous outcome has a skewed distribution or influential extreme values, a mean and standard deviation may not fully represent its shape. The registry does not report distributional diagnostics, transformations, robust methods, or an alternative analysis for the primary outcome.

The primary outcome description calls the result an observed-group analysis. The record does not report whether the analyses followed intention-to-treat principles, how participants were classified if treatment changed, or whether missing data were imputed. These choices can affect what population and treatment effect an estimate represents. Without those details, the posted results cannot establish whether the comparison reflects assignment to a strategy, treatment received, or only the observed participants contributing outcome data.

The secondary outcome is also continuous and is reported as mean and standard deviation. Its spread differs substantially across groups in the posted summaries, so the means should be read with their dispersion information rather than in isolation. The registry does not report model-based analyses for that endpoint. General statistical caution: when variability differs across groups, assumptions about a common variance can affect standard errors and intervals. No claim is made that any particular variance assumption was used by the trial analysis.

Finally, the study is labeled factorial, but a factorial label does not tell the reader which model or contrasts were used. It describes an organizing feature of the design. The registry's pairwise summaries should not be recast as a full factorial analysis without a reported analysis plan and results. The trial's original statistical analysis plan, including model specification, handling of repeated measurements, and any interim analyses, is not reported in the registry record.

11. Confidence Intervals and Precision

The primary mean-difference intervals are broad relative to their point estimates and each includes zero. For immediate methotrexate plus sulfasalazine and hydroxychloroquine versus immediate methotrexate plus etanercept, the estimate is -0.1 and the interval runs from -0.501 to 0.301. For step-up etanercept versus the reference, the estimate is 0.1 and the interval runs from -0.204 to 0.405. For step-up sulfasalazine and hydroxychloroquine versus the reference, the estimate is -0.2 and the interval runs from -0.566 to 0.166.

These intervals allow values on either side of zero. They therefore do not establish a clear direction for any of the individual mean differences. Their width also matters: estimates that are near zero can still be imprecise when the interval includes a meaningful range of positive and negative differences. The registry does not report a threshold for clinical importance, so it is not possible to classify the whole interval as clinically negligible or important based on the record alone.

General explanation: precision depends on the amount of information and variability in the data, as well as the method used to calculate an interval. A confidence interval is not a guarantee that a particular fixed percentage of individual values lie within its endpoints. The confidence level and calculation method for the posted intervals are not reported in the registry record. Standard deviations describe participant-level spread; they should not be mistaken for confidence intervals around group means.

The primary group analysis counts differ, and the standard deviations indicate variation within groups. Both features are relevant when considering how much information supports each comparison. The posted precision does not show that the strategies are equivalent. Demonstrating equivalence or noninferiority would require prespecified margins and a suitable design and analysis, which are not reported in the registry record.

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 planning figures are illustrations based on the observed effect, not the trial's own original design assumptions. The registry record does not report the original sample-size justification. For continuous outcomes, the figures are participants per arm, not a combined total. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is the stated fraction of the observed effect. Time-to-event planning displays, if present, would give total events; these outcomes are not time-to-event outcomes.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one. The 90% column uses a higher chance of detection and therefore generally requires more participants per arm for the same target effect. These are design-planning quantities, not estimates of what the completed trial's results mean.

Rows for planning at 100%, 75%, and 50% of the observed effect ask what sample size would be needed if the target difference were the full observed estimate or a smaller fraction of it. Smaller effects are harder to distinguish from random variation and therefore need more participants to reach the same planned power under otherwise equal assumptions. Where an observed estimate is very small, the resulting planning figures can become very large and should not be read as a recommendation or as evidence that the original trial was inadequately designed.

These calculations are not observed power. They do not tell whether the trial succeeded or failed, and they do not replace interpretation of the estimated differences and confidence intervals. They also rely on simplifying assumptions, including equal allocation and a normal approximation, and use the observed effect as the planning target. The registry does not report whether its original design used these assumptions or any of these effect sizes.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.100; pooled standard deviation σ = 1.433.
2. n = 2 × (1.96 + 0.842)² × 1.433² / -0.100² = 3,223.3, rounded up to 3,224 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.1                      # observed difference in means
sigma <- 1.43295067587303                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(259610)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 3,224 (80% power), 4,316 (90% power)
 75% of observed effect: n per arm = 5,731 (80% power), 7,672 (90% power)
 50% of observed effect: n per arm = 12,894 (80% power), 17,261 (90% power)
power.t.test: 3224.3 
Simulated power at n = 3,224 per arm: 0.803 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The trial includes multiple treatment groups and the registry posts several pairwise comparisons for the primary endpoint, as well as a secondary endpoint. Each additional outcome or contrast creates another opportunity for a result to appear notable even if there is no underlying difference. General statistical explanation: multiplicity procedures can control the chance of false-positive conclusions across a defined family of tests, or a prespecified hierarchy can determine which results are confirmatory. The registry record does not report such a procedure, a hierarchy, or adjusted p-values.

The listed primary p-values are unadjusted. They should be read as individual comparison summaries rather than as multiplicity-controlled evidence for the set of treatment comparisons. The record does not report a global test across groups or tests of main effects and interaction for the factorial design. The interpretation of separate effects of treatment timing and combination choice is therefore unavailable from the registry summaries.

The registry describes the analyzed primary population as randomized participants who completed the study to year 2, and calls the primary outcome an observed-group analysis. It does not report how many randomized participants lacked outcome data, why they lacked data, or how missing values were handled. It also does not report whether imputation, a repeated-measures model, or another method was used. These details matter because a complete-observation analysis can differ from an analysis designed to retain participants with incomplete follow-up.

The record does not specify whether the reported estimates follow intention-to-treat, per-protocol, or treatment-received principles. Nor does it explain how treatment changes or protocol deviations were treated in the analysis. The analysis population description is not enough to determine the estimand, meaning the precise treatment effect the analysis was intended to estimate.

Other statistical-plan details are also absent: the original sample-size justification, the planned model, covariate adjustment, handling of repeated observations, interim analyses, and any prespecified sensitivity analyses are not reported in the registry record. These missing details do not invalidate the posted descriptive results, but they limit assessment of whether the displayed comparisons match the trial's planned confirmatory analysis.

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 0.1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: surgical procedure (2.3%), cancer (2.0%), chest pain (1.6%), other infection (1.6%), diabetes (1.6%).

The registry reports serious adverse events as affected participants and participants at risk within each safety group. For active etanercept with methotrexate, 35 participants were affected among 244 at risk; for active sulfasalazine and hydroxychloroquine with methotrexate, 18 were affected among 132 at risk. For the placebo etanercept group with methotrexate, 32 were affected among 255 at risk; for placebo sulfasalazine and hydroxychloroquine with methotrexate, 16 were affected among 124 at risk. These are group-specific counts, not comparative risk estimates.

Other adverse events are also reported as affected participants and participants at risk: 184 among 244, 99 among 132, 180 among 255, and 89 among 124 in the corresponding groups. The registry lists serious-event terms including Surgical Procedure at 2.3%, Cancer at 2.0%, Chest Pain at 1.6%, Other Infection at 1.6%, Diabetes at 1.6%, and Seizure at 1.6%. The denominator for these term percentages is not reported in the registry record. Death counts are not reported in the registry record.

These safety summaries do not establish that one regimen is safer than another. Interpretation depends on event definitions, exposure duration, ascertainment, and comparative analysis, details not fully reported in the registry record. The counts should be read descriptively rather than as a treatment recommendation.

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

The posted primary data describe mean DAS28-ESR scores in four randomized treatment groups and provide unadjusted pairwise mean differences against methotrexate plus immediate etanercept. Those differences are small in the reported units, and their confidence intervals include zero. The data therefore do not sharply distinguish the compared group means in the posted analysis. The record does not report an equivalence margin, a clinically important difference, or a formal factorial analysis that would support broader conclusions about treatment timing and combination type.

This finding should not be translated into a claim that the strategies are identical. Lack of a clearly separated estimate is not the same as evidence that clinically relevant differences have been excluded. The intervals span positive and negative values, and their interpretation is limited by the absence of the confidence level, analysis method, missing-data details, and multiplicity plan in the registry record.

The reported endpoint is a disease activity score, not a direct measure of all aspects of rheumatoid arthritis. It does not alone describe radiographic progression, adverse events, participant experience, or long-term outcomes. The registry includes a radiographic secondary outcome and adverse-event counts, but those records also have limitations in reported analyses and context. No recommendation about which therapy an individual should use follows from these summaries.

The trial's randomized factorial design is relevant to causal comparisons, but the registry's posted pairwise summaries do not show how allocation was analyzed across the factorial structure. The reported primary analysis population is restricted to participants who completed the study to year 2, and the handling of missing observations is not specified. Consequently, the results characterize the posted observed groups; the registry record alone does not establish how the estimates would change under a different analysis population or missing-data approach.

A balanced reading is that the registry reports broadly similar group means with uncertain pairwise differences for the stated primary measure, alongside a secondary radiographic measure and safety summaries. That is a description of the posted results, not proof of no effect, proof of equivalence, or a judgment about an individual's treatment.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it combines a treatment-choice question with a treatment-timing question in a randomized factorial design. Such a design can address more than a simple comparison of two regimens, but only if the analysis reports how the factors and their possible interaction were evaluated. The registry identifies the factorial model but does not post those analyses. The distinction between design structure and reported analysis is important when interpreting the pairwise summaries.

The primary outcome is a continuous disease activity score, reported with means and standard deviations. That allows readers to see both the estimated group averages and the observed variability. The uncertainty intervals are especially useful because the point estimates alone could look more definitive than the data warrant. In this case, the intervals include zero and allow differences in either direction, emphasizing uncertainty rather than a clear separation.

The trial also illustrates why a secondary outcome and safety counts need separate interpretation. Radiographic progression measures a different aspect of disease than DAS28-ESR, while adverse-event counts require context about exposure, definitions, and the comparative design. Neither can simply be substituted for the primary endpoint. The registry's limited reporting of multiplicity and analysis populations further shows why a list of estimates is not the same as a complete statistical analysis plan.

Finally, the planning illustrations highlight a general feature of trial design: detecting smaller effects generally takes more participants under the same assumptions. Those illustrations use observed effects and are not the original design justification. Keeping planning quantities distinct from trial outcomes prevents an incorrect inference about whether a study had adequate observed power. Together, these features make the trial useful for learning how design, estimation, precision, and reporting completeness shape interpretation.

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.

The registry record contains several trial-specific reporting gaps. The primary outcome description says that the analysis is based on randomized participants who completed the study to year 2, but the record does not explain the treatment of participants with incomplete follow-up or missing endpoint measurements. The posted group counts vary, and the registry does not describe the reasons for those differences. This limits assessment of selection and missing-data effects.

Although the trial is labeled factorial, the posted comparisons use one group as a reference and do not report factorial main effects or an interaction analysis. The record also does not report a global comparison across groups, the prespecified primary contrast, an adjustment for multiple comparisons, or whether the displayed inferential analyses were prespecified. These omissions make it difficult to determine the confirmatory status of individual pairwise findings.

The confidence-interval level and the statistical model used to construct the estimates are not reported. The record does not state whether covariates were included, how repeated measurements were handled, or whether assumptions were checked. It does not provide a clinically important threshold for the DAS28-ESR differences. As a result, statistical precision cannot be directly mapped to clinical importance.

The secondary radiographic outcome has posted descriptive summaries, but the registry lists no reported analyses. The safety data provide affected counts and at-risk counts, as well as percentages for selected serious-event terms, but do not describe exposure time, detailed event definitions, or the denominator for the term percentages. Death counts are not reported in the registry record.

Finally, the planning sample-size illustrations are based on observed effects and stated assumptions, not the trial's original design. The original justification and analysis plan are not reported. These limitations concern what can be inferred from the registry record and do not, on their own, establish that the trial conduct or analyses were inadequate.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Treatment of Early Aggressive Rheumatoid Arthritis (TEAR) — NCT00259610.
• Registry record last updated 2014-07-17; status last verified 2013-10.
• 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.

22. Record Summary

TEAR is a completed phase 4 randomized factorial trial sponsored by University of Alabama at Birmingham, with enrollment of 755 and quadruple masking recorded. The primary outcome is mean DAS28-ESR change between weeks 48 and 102 in participants described as randomized and completing the study to year 2.

The posted group means are close, and the three unadjusted primary mean-difference intervals include zero. The registry also reports a secondary radiographic progression outcome and group-specific adverse-event summaries. It does not report a factorial analysis, multiplicity plan, detailed missing-data methods, confidence-interval level, or original sample-size justification. Interpretation is therefore best anchored to the observed summaries and their uncertainty, without treating them as proof of equivalence or as a treatment recommendation.