A Rheumatoid Arthritis Study in Participants on a Background Treatment of Methotrexate: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Rheumatoid Arthritis Study in Participants on a Background Treatment of Methotrexate (NCT01198002), a randomized phase 3 study. The primary outcome is Percentage of Participants With American College of Rheumatology 20% Response (ACR20) at Week 24.

2. Clinical Question

3. Trial Design

This was a Phase 3, multicenter, randomized, double-blind, placebo-controlled, parallel-group study. It enrolled participants with moderate to severe rheumatoid arthritis who had an inadequate response to methotrexate therapy. Enrollment was 1041. The registry lists LY2127399, two placebo schedules, and methotrexate among the interventions, and the primary comparison uses placebo as the comparator while participants remained on background methotrexate.

The registry describes three study periods: a 52-week blinded treatment period, an additional 48-week unblinded treatment period, and a 48-week post-treatment follow-up. The primary endpoint was measured through Week 24, within the first treatment period. Arm descriptions indicate that participants could receive different dosing schedules and that some participants were assigned different treatments at later study stages. Those later-stage arrangements do not change the stated Week 24 primary comparison, but they matter when interpreting safety groups reported across periods.

The record gives a start date of 2010-12 and primary completion date of 2012-12. Its status is terminated. The reason for termination and whether termination affected the planned analyses are not reported in the registry record. The original protocol’s sample-size justification, planned interim analyses, statistical analysis plan, and detailed randomization procedures are not reported in the registry record. The study’s stated design features therefore describe its broad structure, but do not fill in those unreported details.

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: Study had a blinded Treatment Period 1 (Weeks 0-52), a non-blinded Treatment Period 2 (Weeks 52-100) and a post-treatment follow-up (24-48 weeks in length). All participants were assessed for nonresponse at Week 16 with non-responders (NR) defined as participants with \<20% improvement from baseline in both tender and swollen joint counts.

Treatment Period 1 (Weeks 0-52)

Reasons for not completing this period:

Treatment Period 2 (Weeks 52-100)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized participants with evaluable ACR20 responder data. If participant's CRP was missing, last post-baseline value was used. If ACR was missing after carrying forward CRP, last post-baseline ACR response was used. Data after Week 16 for Week 16 NR were not included.

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: All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With American College of Rheumatology 20% Response (ACR20) at Week 24, measured over Baseline through 24 weeks.

The primary endpoint was the percentage of participants with an American College of Rheumatology 20% response, or ACR20, at Week 24. ACR20 is a composite response measure: participants had to achieve at least 20% improvement from baseline in both tender and swollen joint counts, and at least 20% improvement in three or more of five other criteria. Those criteria include participant and physician global assessments of disease activity, the Health Assessment Questionnaire-Disability Index, joint pain, and C-reactive protein.

A composite endpoint combines several dimensions of a condition into one responder classification. This can capture more than a single symptom or laboratory measure, while making the response rule explicit. Here, an ACR20 response required improvement across joint counts as well as a minimum number of additional criteria; a change in only one component would not meet the stated definition.

The registry defines the outcome as the number of responders divided by the number of participants treated, expressed as a percentage. It also specifies handling for some missing measurements: if C-reactive protein was missing, the last post-baseline value was used; if ACR response remained missing after that step, the last post-baseline ACR response was used. Participants who were nonresponders at Week 16, and those who discontinued study treatment, were classified as nonresponders from that time onward. Data after Week 16 for Week 16 nonresponders were not included.

7. Results Posted in the Registry

• 120 mg LY2127399: 29.7% (98/330) versus 25.1% (84/335) on control; risk difference 4.6 percentage points (95% CI -2.1 to 11.4), risk ratio 1.18 (0.92–1.52); unadjusted two-proportion z-test p = 0.181.
• 90 mg LY2127399: 32.8% (109/332) versus 25.1% (84/335) on control; risk difference 7.8 percentage points (95% CI 0.9 to 14.6), risk ratio 1.31 (1.03–1.67); unadjusted two-proportion z-test p = 0.027.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants With Change From Baseline in mTSS Less Than or Equal to (≤) 0

• 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:
  • 120 mg LY2127399: 61.0% (180/295) versus 56.2% (172/306) on control; risk difference 4.8 percentage points (95% CI -3.1 to 12.7), risk ratio 1.09 (0.95–1.24); unadjusted two-proportion z-test p = 0.232.
  • 90 mg LY2127399: 61.8% (188/304) versus 56.2% (172/306) on control; risk difference 5.6 percentage points (95% CI -2.2 to 13.4), risk ratio 1.10 (0.96–1.26); unadjusted two-proportion z-test p = 0.157.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 120 mg LY2127399 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 90 mg LY2127399 and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Developing Anti-LY2127399 Antibodies

• 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:
  • 120 mg LY2127399: 3.8% (13/344) versus 4.9% (17/347) on control; risk difference -1.1 percentage points (95% CI -4.2 to 1.9), risk ratio 0.77 (0.38–1.56); unadjusted two-proportion z-test p = 0.470.
  • 90 mg LY2127399: 1.5% (5/344) versus 4.9% (17/347) on control; risk difference -3.4 percentage points (95% CI -6.0 to -0.8), risk ratio 0.30 (0.11–0.80); unadjusted two-proportion z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 120 mg LY2127399 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 lower for 90 mg LY2127399 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With No Structural Progression at Week 52

• 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:
  • 120 mg LY2127399: 55.6% (164/295) versus 53.9% (165/306) on control; risk difference 1.7 percentage points (95% CI -6.3 to 9.6), risk ratio 1.03 (0.89–1.19); unadjusted two-proportion z-test p = 0.681.
  • 90 mg LY2127399: 57.6% (175/304) versus 53.9% (165/306) on control; risk difference 3.6 percentage points (95% CI -4.2 to 11.5), risk ratio 1.07 (0.93–1.23); unadjusted two-proportion z-test p = 0.365.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 120 mg LY2127399 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 90 mg LY2127399 and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad range of secondary outcomes, including additional ACR response thresholds, disease activity, physical function, fatigue, pain, morning stiffness, and structural change. It reports 27 secondary outcomes, while detailed analyses are not listed for them. The posted secondary summaries that have comparison calculations cover structural measures at Week 24 and Week 52, and development of anti-LY2127399 antibodies through Week 52. Their overall pattern is mixed in precision: some intervention-group percentages are higher than placebo, but several unadjusted confidence intervals include no difference; one comparison for antibody development has an interval below zero.

This pattern can be considered alongside the primary endpoint, but it should not be treated as independent confirmation of the ACR20 comparison. Secondary outcomes address different dimensions, time points, or biological measures. Agreement in direction may provide context, while disagreement or imprecision can reflect distinct outcome definitions and information levels. No single secondary measure replaces the primary endpoint’s prespecified clinical response definition.

Unadjusted secondary comparisons carry less inferential weight when many outcomes and comparisons are examined. With multiple tests, the chance of at least one apparently unusual result can increase, even if all underlying null hypotheses are true. General statistical practice addresses this through a planned testing hierarchy or adjustment, but neither the multiplicity plan nor adjusted secondary analyses are reported in the registry record. The posted secondary p-values and intervals should therefore be viewed as exploratory descriptions rather than a family of confirmatory conclusions.

The secondary outcome list also includes measures for which results are not present in the details. The record does not report enough information to infer that unposted outcomes were null, favorable, or unfavorable. The appropriate overall reading is that the secondary data provide additional, varied measurements, but their incomplete analysis reporting and unreported multiplicity handling limit how strongly they can support a unified efficacy interpretation.

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

• Percentage of Participants With American College of Rheumatology 50% (ACR50) and 70% (ACR70) Response
• Change From Baseline in Disease Activity Score Based on 28 Joint Count and C-Reactive Protein Level (DAS28-CRP)
• Percentage of Participants With DAS28-CRP Based European League Against Rheumatism (EULAR) Response
• Change From Baseline in Medical Outcomes Study 36-Item Short Form (SF-36) Health Survey Domain Scores and Summary Scores
• Change From Baseline in Brief Fatigue Inventory (BFI) Individual Items and Impact Score
• Change From Baseline in Duration of Morning Stiffness (Minutes)
• Change From Baseline in Brief Pain Inventory Short Form (BPI-SF) Individual Items and Interference Scores
• Percentage of Participants With Major Clinical Response (MCR) During 52 Weeks

9. Statistical Interpretation

10. Statistical Methods Explained

Binary outcomes, confidence intervals, and p-values

The primary outcome is binary at the participant level: each participant is classified as an ACR20 responder or nonresponder at the endpoint. The arm-level percentage expresses the fraction classified as responders. A risk difference compares two such fractions by subtracting the comparator risk from the intervention risk. It is expressed on a proportion scale, so zero represents equal response proportions; a positive value means the intervention proportion is higher in that comparison, and a negative value means it is lower.

For 120 mg LY2127399 versus placebo, the recalculated risk difference is 0.046, with a 95% confidence interval from -0.021 to 0.114. For 90 mg LY2127399 versus placebo, it is 0.078, with a 95% confidence interval from 0.009 to 0.146. These are unadjusted recalculations from the posted arm summaries. They should not be mistaken for an adjusted model estimate or for the sponsor’s reported primary analysis. The registry’s discrepancy indicator is false, but a detailed sponsor analysis is not reported in the registry record.

A relative risk compares the response probability in one group with that in another. An odds ratio compares response odds rather than response probabilities. Both are alternative ways of expressing a binary-outcome contrast, and their numerical values are not directly interchangeable with a risk difference. The recalculated relative-risk and odds-ratio estimates are available for the dose comparisons, but no sponsor-reported inferential analysis accompanies them in the registry record. The choice of effect measure changes the scale of the comparison, not the underlying participant outcomes.

A confidence interval describes a range of values compatible with the observed data under the method used to calculate it. A narrower interval indicates greater precision for that estimate; an interval spanning zero for a risk difference includes equal response proportions among its compatible values. A p-value measures how unusual the observed comparison, or a more extreme one, would be under a specified null model. It does not measure the probability that the null hypothesis is true, nor does it report the size or clinical importance of an effect. The posted p-values are unadjusted recalculations.

What the response rule and missing-data handling mean

ACR20 is a composite responder definition rather than a single measurement. The rule requires improvement in both joint-count components plus improvement in at least three of the other five listed criteria. Participants must meet the combined rule to count as responders. This yields a result that reflects the specified collection of measures, but it does not show which component contributed most to a participant’s classification.

The registry describes carrying forward the last post-baseline C-reactive protein value when that measure is missing, then carrying forward the last post-baseline ACR response if ACR information remains missing. It also classifies participants who discontinue treatment as nonresponders from discontinuation onward, and classifies Week 16 nonresponders as nonresponders thereafter. Such rules determine how incomplete follow-up contributes to the endpoint. The registry does not report sensitivity analyses comparing these rules with other missing-data approaches.

What is not specified

The registry does not report the original statistical analysis plan, the sponsor’s detailed analysis model, the planned significance threshold for the primary endpoint, the handling of multiplicity, or an interim-analysis plan. The number of reported analyses is zero, and detailed reported analyses are not listed for the secondary outcomes. Consequently, the recalculated comparisons should be treated as supplementary readings of the posted arm summaries, rather than substitutes for a prespecified analysis. General statistical principles explain how these estimates work, but cannot establish which methods the trial originally intended to use.

General statistical concept: random allocation is intended to make treatment groups comparable on average, while masking is intended to reduce the influence of treatment knowledge on participant care and outcome assessment. The registry identifies the study as randomized and double-blind, but does not report enough implementation detail to assess how allocation concealment or masking was maintained. Statistical interpretation should remain tied to the reported outcome definitions, group summaries, and comparison calculations.

11. Confidence Intervals and Precision

The confidence intervals communicate uncertainty around the unadjusted risk-difference estimates. For 120 mg LY2127399 versus placebo, the estimate is 0.046 and the 95% confidence interval ranges from -0.021 to 0.114. Because this interval crosses zero, the posted summary statistics do not pin down the direction of the difference with the same precision as an interval entirely on one side of zero. Its range remains compatible with a lower response proportion in the LY2127399 group, little or no difference, or a higher response proportion.

For 90 mg LY2127399 versus placebo, the estimate is 0.078 and the 95% confidence interval ranges from 0.009 to 0.146. This unadjusted interval lies above zero, but still spans a range of possible effect sizes. It should be interpreted alongside the unadjusted nature of the recalculation and the absence of reported multiplicity procedures and sponsor analysis details. Interval position alone does not answer whether a result was confirmatory under the trial’s original analysis plan.

A confidence interval is not a guarantee that the true effect lies within its endpoints. In general, it describes the uncertainty associated with a statistical procedure applied to the observed data. Its width reflects both the observed information and the method used. The registry does not post confidence intervals for the arm-specific percentages themselves. These comparison intervals therefore concern differences between groups, not the precision of each percentage viewed separately.

Precision is also limited by the outcome population and data rules. The primary outcome population is evaluable ACR20 responder data, and the stated nonresponder and carry-forward rules affect which participants contribute to the endpoint classification. The registry does not give a sensitivity analysis showing how alternative missing-data assumptions would change the intervals. Thus, the intervals describe the recalculated comparisons under the posted summaries; they do not cover uncertainty arising from unreported analytic choices.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations describe planning for a future two-group comparison using the observed effect as a reference point. For this binary outcome, the entries are participants per arm, not total events. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row represents planning to detect the stated fraction of the observed effect: 100%, 75%, or 50%.

The 80% power column gives the number of participants per arm that the stated calculation would require for an 80% chance of detecting the specified effect under its assumptions. The 90% power column gives the corresponding number per arm for a 90% chance. Power is a design probability under a particular effect and set of assumptions; it does not describe the probability that a conclusion is correct. Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants.

For example, the primary comparison planning entries differ by dose because the observed effect sizes differ. The 90 mg comparison lists 536 participants per arm for 80% power and 717 for 90% power when planning for 100% of the observed effect. The corresponding 120 mg entries are 1,460 and 1,954. Planning for 75% or 50% of the observed effect requires larger per-arm counts in both comparisons. These values are illustrations based on the posted outcome summaries, not the trial’s original design calculation. The original sample-size justification is not reported in the registry record.

These planning figures are not observed power. They should not be used to reinterpret the trial as having been designed around the observed effect, because the registry does not report that design assumption. The calculations also rely on the stated normal approximation and equal allocation. They are useful for understanding how a future study’s required enrollment changes with the target effect and desired power, not for replacing the trial’s confidence intervals or reported outcomes.

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 = 0.251; treatment proportion p₁ = 0.297; average p̄ = 0.274.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6307 = 1.2361.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6298 = 0.5301.
4. n = (1.2361 + 0.5301)² / (0.0462)² = 1,459.9, rounded up to 1,460 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 <- 0.250746268656716                          # control proportion
p1 <- 0.296969696969697                          # 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(1198002)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,460 (80% power), 1,954 (90% power)
 75% of observed effect: n per arm = 2,562 (80% power), 3,429 (90% power)
 50% of observed effect: n per arm = 5,686 (80% power), 7,611 (90% power)
power.prop.test: 1459.9 
Simulated power at n = 1,460 per arm: 0.805 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record does not report how the trial handled multiplicity. This matters because the record includes a primary comparison involving two LY2127399 dose groups against placebo and a large set of secondary outcomes. Testing multiple hypotheses without adjustment or a prespecified hierarchy can increase the chance of at least one apparently notable result arising by chance. The record does not identify a primary testing sequence, family of hypotheses, adjusted significance threshold, or multiplicity-adjusted p-values.

The available comparison p-values are unadjusted recalculations from the posted summary statistics. They do not account for other comparisons or outcomes. In particular, the nominal p-value for the 90 mg primary comparison should not be interpreted as a multiplicity-controlled conclusion. The record also lists no reported analysis entries, so the sponsor’s planned model and inferential results cannot be checked against these simple recalculations.

Missing data are addressed in part by the endpoint description. Missing C-reactive protein values are replaced with the last post-baseline value; if ACR response is still missing, the last post-baseline ACR response is used. Participants who discontinue treatment are defined as nonresponders from that time onward, and Week 16 nonresponders remain nonresponders in subsequent classification. Data after Week 16 for Week 16 nonresponders were not included. These are substantive analysis rules, not merely data-cleaning details, because they affect who counts as a responder.

The registry does not report sensitivity analyses that test how robust the result is to alternative assumptions about missing outcomes. Nor does it give a detailed account of missingness by arm or reasons for missing values for the primary endpoint. The primary outcome population is described as randomized participants with evaluable responder data, but the record does not provide enough analysis detail to reconstruct all participant flow into the endpoint calculation.

The trial is marked terminated, but its reason for termination and any consequences for outcome collection or planned testing are not reported in the registry record. The record also does not report an interim-analysis plan. These reporting gaps do not determine what happened, but they restrict evaluation of the analysis process and the confirmatory status of the posted comparisons.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: femur fracture (7.4%), pyelonephritis acute (3.7%), obliterative bronchiolitis (3.7%), bladder transitional cell carcinoma stage iii (3.2%), rheumatoid arthritis (2.4%).

The registry reports serious adverse-event counts and counts for other adverse events in groups defined by treatment and study period. For example, during randomized Treatment Period 1, the serious adverse-event counts were 19 among 345 at risk in the LY 120 mg Q4W group, 17 among 345 at risk in the LY 90 mg Q2W group, and 17 among 348 at risk in the placebo group. The corresponding counts for other adverse events were 137 among 345, 117 among 345, and 129 among 348. These are counts as posted, not recalculated event rates.

Other groups describe rescue, Treatment Period 2, and follow-up, including participants whose treatment changed. Their denominators and exposure periods differ, so the groups should not be read as if they were one randomized comparison with identical follow-up. The registry lists serious adverse-event terms with percentages, including femur fracture, acute pyelonephritis, obliterative bronchiolitis, bladder transitional cell carcinoma stage iii, rheumatoid arthritis, and cellulitis. The denominator and calculation method for those listed percentages are not reported in the registry record.

Deaths are not reported in the posted group entries. Adverse-event counts alone do not establish causation or comparative risk. Interpretation would require details such as event definitions, exposure time, adjudication, and the sponsor’s safety analysis, which are not reported in the registry record.

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

The Week 24 result describes the percentage of participants classified as ACR20 responders under the registry’s composite definition and missing-data rules. The posted response percentage is higher in each LY2127399 arm than in the placebo arm. The recalculated unadjusted risk-difference interval for 120 mg includes zero, while the corresponding interval for 90 mg is above zero. Those summaries convey the observed pattern and its statistical precision, but they do not replace the trial’s sponsor analysis or answer how multiplicity was handled.

The endpoint does not represent every potential benefit or harm, and it does not show which individual component of the composite drove the response classification. The primary result is measured through Week 24; it cannot by itself describe results over the full treatment and follow-up periods. Secondary outcomes cover other measures and time points, but the registry does not report a complete set of detailed secondary analyses or a multiplicity plan.

Nor does a p-value give the probability that an intervention works or fails. A p-value is conditional on a statistical model and null hypothesis, and the posted values are unadjusted recalculations. The confidence intervals likewise express uncertainty for those calculations, not certainty about the result. An interval that excludes zero does not resolve the unreported analysis choices or establish clinical importance.

The terminated status is a registry status, not an explanation of the study’s findings. The reason for termination is not reported in the registry record, so it should not be used to infer that the results were positive, negative, incomplete, or unsafe. Similarly, the serious adverse-event counts are descriptive and do not show whether events were caused by treatment. The record supports a careful description of the posted data, while important details needed for a definitive overall interpretation remain unreported.

17. Why This Trial Matters Statistically

This trial illustrates why interpretation depends on more than comparing arm percentages. The primary outcome uses a structured composite response rule, and the registry supplies group percentages as well as summary statistics from which simple pairwise comparisons can be recalculated. Those comparisons show how the estimated effect and its uncertainty differ across dose groups, while also making clear that an unadjusted analysis is not equivalent to the study’s prespecified inferential analysis.

The record also highlights the distinction between response magnitude and precision. A point estimate gives one summary of the observed contrast; its confidence interval conveys how broadly the data support possible values under the calculation method. The two primary comparisons have different interval patterns. Reading those intervals alongside the reported percentages avoids treating the point estimates or p-values as complete descriptions on their own.

Another statistical issue is the interaction between endpoint definitions, missing data, and follow-up. The ACR20 classification combines joint counts with other clinical and laboratory criteria. The registry also defines how missing measurements, Week 16 nonresponse, and treatment discontinuation affect responder status. These rules shape the estimand that the reported percentage describes. Without sensitivity analyses, it is difficult to assess how dependent the results are on those choices.

Finally, the trial provides a practical example of why multiplicity and reporting transparency matter. Multiple doses and many secondary outcomes create a broader inferential context than one isolated p-value. The registry record does not describe a testing hierarchy or sponsor-reported analysis results. That omission limits the weight that can be placed on nominal secondary or unadjusted primary comparisons. The statistical lesson is not to discard the posted results, but to distinguish transparent descriptive evidence from conclusions that require a complete analysis plan and report.

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 limitations are specific to the available record. First, the trial status is terminated, but the reason and its implications for planned follow-up or analysis are not reported in the registry record. The record describes a longer treatment and follow-up structure than the Week 24 primary endpoint, but the primary comparison alone does not describe outcomes across those later periods.

Second, the registry gives an enrollment figure of 1041, while the primary outcome is defined for randomized participants with evaluable ACR20 data and the posted arm summaries have their own denominators. The record does not provide enough participant-flow detail to reconcile those populations fully. It also does not report a complete account of missing primary outcome data by group.

Third, the primary outcome’s missing-data rules are specified, but sensitivity analyses using alternative assumptions are not reported. Because discontinuation and Week 16 nonresponse lead to nonresponder classifications, the endpoint depends on those rules. The record does not show whether different reasonable approaches would change the results.

Fourth, the comparisons discussed are unadjusted recalculations, and the registry does not report the sponsor’s analysis model, multiplicity plan, original sample-size justification, or interim-analysis plan. The status and broad design features are available, but detailed methods needed to verify the intended confirmatory analysis are not. The arm descriptions are also incomplete, limiting reconstruction of some treatment changes and dosing details.

Finally, safety groups span treatment periods and changing assignments, and the registry does not report exposure-adjusted rates or a complete safety analysis. Counts from groups with differing follow-up should not be treated as directly comparable risks. These limitations constrain interpretation of the record; they do not establish what unreported analyses or outcomes would have shown.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Rheumatoid Arthritis Study in Participants on a Background Treatment of Methotrexate — NCT01198002.
• Registry record last updated 2018-05-08; status last verified 2018-05.
• Results first posted 2018-05-08.
• 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 record describes a Phase 3, multicenter, randomized, double-blind, placebo-controlled study of LY2127399 in participants with moderate to severe rheumatoid arthritis and an inadequate response to methotrexate. Enrollment was 1041, and the record lists the study as terminated. The primary endpoint was ACR20 response at Week 24. Posted response percentages were 29.7 for 120 mg LY2127399, 32.8 for 90 mg LY2127399, and 25.1 for placebo.

Unadjusted recalculations from the posted summaries give different confidence-interval patterns for the two dose comparisons. The record also contains secondary outcome summaries and adverse-event counts, but does not report sponsor analysis results, multiplicity handling, the reason for termination, or the original sample-size justification. These omissions limit confirmatory interpretation of the posted comparisons.