Global Study to Assess the Safety and Effectiveness of Edoxaban (DU-176b) vs Standard Practice of Dosing With Warfarin in Patients With Atrial Fibrillation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Global Study to Assess the Safety and Effectiveness of Edoxaban (DU-176b) vs Standard Practice of Dosing With Warfarin in Patients With Atrial Fibrillation (NCT00781391), a randomized phase 3 study. The primary outcome is Compare Edoxaban to Warfarin for Composite of Stroke and Systemic Embolic Events (SEE)..

2. Clinical Question

The trial was conducted in people with atrial fibrillation, a population for whom stroke and systemic embolic events are clinically important outcomes. The primary endpoint combines stroke with systemic embolic events (SEE), so it captures more than one type of thromboembolic event in a single outcome. The registry identifies stroke, atrial fibrillation, and embolism among the study conditions.

The registry lists three treatment groups: high-dose edoxaban, low-dose edoxaban, and warfarin. The placebo tablets paired with active treatment supported the double-dummy design. In this design, participants take matching active and placebo preparations so that treatment assignment can remain masked despite differences in the study drugs. That is a general description of the design; details of how masking was maintained are not reported in the registry record.

The primary endpoint was evaluated during the on-treatment period in the mITT population, rather than across the entire overall study period. The endpoint description specifies median study drug exposure of 2.5 years and median follow-up of 2.8 year. The registry also lists secondary outcomes involving cardiovascular mortality, all-cause mortality, major adverse cardiac events, and adjudicated bleeding events. The statistical question is about comparative event experience under the trial’s stated endpoint and analysis framework, not about a recommendation for an individual patient.

3. Trial Design

This was a phase 3, randomized, double-blind, double-dummy, parallel-group, multi-center, multi-national study. The registry classifies allocation as randomized, masking as quadruple, and the model as parallel. The study was sponsored by Daiichi Sankyo and is recorded as completed. Enrollment is listed as 21105. The registry start is 2008-11, and primary completion is 2013-04.

Participants were assigned to high-dose edoxaban, low-dose edoxaban, or warfarin. The high-dose regimen is described as edoxaban 60mg with placebo warfarin; the low-dose regimen as edoxaban 30mg with placebo warfarin; and the warfarin group as warfarin with placebo edoxaban. The registry’s primary outcome arm counts are 7002.0 for low-dose edoxaban, 7012.0 for high-dose edoxaban, and 7012.0 for warfarin. These are arm-specific figures for the primary outcome; the overall enrollment figure is reported separately.

The primary endpoint was a composite of stroke and SEE, recorded as the number of participants with an event. Its timeframe is the on-treatment period, defined in the endpoint description as the period taking study drug and up to 3 days after the last dose. The primary analysis population was the mITT set, defined as randomized subjects who received one or more doses of study drug. Median study drug exposure was 2.5 years, with median follow-up of 2.8 year.

The brief summary says the expected duration of the study was 24 months. That statement is a planned duration in the summary, not a description of the actual follow-up for each participant. The actual endpoint timeframe and median exposure and follow-up are reported separately. Original sample-size assumptions, the trial’s sample-size justification, and details of the statistical analysis plan are not reported in the registry record. The registry includes sponsor analyses using Cox proportional hazards models for the primary endpoint, but it does not report the non-inferiority margin in the information available for this account.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: mITT (modified Intent To Treat) Analysis set; which included randomized subjects who received 1 or more dose of study drug. The time period included the subject was taking study drug and up to 3 days after their last dose (On-Treatment ).

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 Compare Edoxaban to Warfarin for Composite of Stroke and Systemic Embolic Events (SEE)., measured over on-treatment period 2.5 years of median study drug exposure and 2.8 year of median follow-up.

The primary endpoint combines stroke and systemic embolic events (SEE), counted as participants with at least one qualifying event during the on-treatment period. A composite endpoint can represent a broader clinical outcome than any single component and can increase the number of events available for analysis. That is a general statistical rationale for composite outcomes; it does not establish that each component is equally important or that the treatment effects are the same for each component.

The endpoint is defined for the mITT analysis population: randomized subjects who received at least one dose of study drug. The on-treatment time period included the time a subject was taking study drug and up to 3 days after the last dose. This definition makes the primary outcome specifically about events during or shortly after active study-drug exposure. It differs from the overall-study-period timeframes used for the secondary composite outcomes.

The registry reports event counts by treatment arm and also a sponsor time-to-event analysis. Counts indicate how many participants experienced an event, while a time-to-event method considers the timing of events and can account for differing follow-up times under its analysis framework. These summaries answer related but not identical statistical questions. The registry lists the primary outcome as a non-inferiority analysis, but the non-inferiority margin and other details of the original analysis plan are not reported in the registry record.

For interpretation, the endpoint should be read as a composite measure within a defined population and timeframe, rather than as a direct account of every stroke or embolic event separately. Component-specific primary endpoint results are not reported in the registry record.

7. Results Posted in the Registry

• High Dose Edoxaban/Placebo Warfarin: 2.6% (182/7012) versus 3.6% (253/7002) on control; risk difference -1.0 percentage points (95% CI -1.6 to -0.4), risk ratio 0.72 (0.60–0.87); unadjusted two-proportion z-test p = <0.001.
• Warfarin/Placebo Edoxaban: 3.3% (232/7012) versus 3.6% (253/7002) on control; risk difference -0.3 percentage points (95% CI -0.9 to 0.3), risk ratio 0.92 (0.77–1.09); unadjusted two-proportion z-test p = 0.324.

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.

Compare Edoxaban to Warfarin for Composite of Stroke, Systemic Embolic Event (SEE), and Cardiovascular (CV) Mortality

• 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:
  • High Dose Edoxaban/Placebo Warfarin: 10.3% (728/7035) versus 11.3% (796/7034) on control; risk difference -1.0 percentage points (95% CI -2.0 to 0.1), risk ratio 0.91 (0.83–1.01); unadjusted two-proportion z-test p = 0.065.
  • Warfarin/Placebo Edoxaban: 11.8% (831/7036) versus 11.3% (796/7034) on control; risk difference 0.5 percentage points (95% CI -0.6 to 1.6), risk ratio 1.04 (0.95–1.14); unadjusted two-proportion z-test p = 0.359.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between High Dose Edoxaban/Placebo Warfarin 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 Warfarin/Placebo Edoxaban and the control. The interval gives the range of effects that remain compatible with the data.

Compare Edoxaban to Warfarin for Composite of Stroke, SEE, and All-cause Mortality

• 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:
  • High Dose Edoxaban/Placebo Warfarin: 13.5% (949/7035) versus 14.0% (985/7034) on control; risk difference -0.5 percentage points (95% CI -1.7 to 0.6), risk ratio 0.96 (0.89–1.05); unadjusted two-proportion z-test p = 0.376.
  • Warfarin/Placebo Edoxaban: 14.9% (1046/7036) versus 14.0% (985/7034) on control; risk difference 0.9 percentage points (95% CI -0.3 to 2.0), risk ratio 1.06 (0.98–1.15); unadjusted two-proportion z-test p = 0.145.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between High Dose Edoxaban/Placebo Warfarin 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 Warfarin/Placebo Edoxaban and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering composites that add cardiovascular mortality or all-cause mortality to stroke and SEE, a major adverse cardiac event composite, and adjudicated bleeding events. Detailed results are available for the two mortality-related composites described in the posted outcome information. The remaining listed secondary outcomes’ detailed estimates are not reported in the registry record.

For the reported secondary analyses, the sponsor provides log-rank time-to-event results for the high-dose edoxaban versus warfarin comparison. These are distinct outcomes and use an overall-study-period timeframe, unlike the primary endpoint’s on-treatment timeframe. The posted count-based comparisons and the sponsor’s time-to-event results are therefore not direct duplicates of the primary analysis. The secondary outcomes broaden the picture beyond stroke and SEE alone, but they do not replace the primary endpoint or its defined population and follow-up period.

Across the reported secondary results, the findings are not uniformly conclusive across all simple re-calculations and outcomes. The sponsor’s reported time-to-event analyses and the count-based re-calculations can also differ because they use different methods and effect measures. Interpret those results in the context of their own endpoint definitions and analysis methods rather than pooling them into a single overall conclusion.

Unadjusted secondary results carry less weight because testing multiple outcomes and comparisons increases the opportunity for chance findings. The registry does not report whether multiplicity adjustments were planned or applied, or the complete hierarchy of hypotheses. Secondary p-values should therefore not be treated as if each were the sole prespecified test. They can inform the pattern of outcomes, but confirmation requires attention to the analysis plan, multiplicity, and the clinical meaning of each endpoint.

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

• Compare Edoxaban to Warfarin for Composite of Stroke, Systemic Embolic Event (SEE), and Cardiovascular (CV) Mortality
• Compare Edoxaban to Warfarin for Major Adverse Cardiac Event (MACE): a Composite of Non-fatal MI, Non-fatal Stroke, Non-fatal SEE, and Death Due to CV Cause or Bleeding
• Compare Edoxaban to Warfarin for Composite of Stroke, SEE, and All-cause Mortality
• Adjudicated Bleeding Events

9. Statistical Interpretation

10. Statistical Methods Explained

What does the event count describe?

The primary outcome is presented as the number of participants with an event. The arm counts tell the reader how many participants met the composite endpoint within the stated population and timeframe. A count alone does not incorporate the exact timing of events. It also does not show whether events occurred early or late in follow-up, or how censoring was handled in the time-to-event analyses.

The re-calculated comparisons use posted summary counts to estimate unadjusted risk differences. A risk difference expresses the difference between the observed event proportions for two arms. Negative values in the reported comparisons indicate that the event proportion was lower in the edoxaban arm than in the warfarin arm for that comparison. These are simple, unadjusted re-calculations and are not a substitute for the sponsor’s model-based analysis. Since a discrepancy is recorded, the sponsor’s own analysis takes precedence.

How does a Cox model differ?

The registry reports Cox proportional hazards models for the sponsor’s primary comparisons. In general, a Cox model analyzes the time until an event and compares the event hazard between groups over follow-up. A hazard ratio below 1 indicates a lower estimated hazard in the first-listed group relative to the comparator under the model; a value above 1 indicates a higher estimated hazard. A hazard ratio is not a risk difference and should not be read as a direct difference in the percentage of participants who experienced an event.

The proportional-hazards model relies on assumptions about the relationship between hazards over time. Whether those assumptions were checked, and how the model handled covariates or missing observations, is not reported in the registry record. The registry records the endpoint as a non-inferiority analysis, but the margin and the detailed decision procedure are not reported. For non-inferiority, the confidence interval must be interpreted against a prespecified margin; the p-value by itself is not sufficient to reconstruct that determination.

What does the confidence interval add?

A confidence interval describes the range of effect estimates compatible with the data under the method’s assumptions and gives information about precision. A narrow interval is more precise than a wide interval, while an interval spanning values on either side of a null effect can leave uncertainty about the direction of the difference. The registry reports 97.5% confidence intervals for the primary Cox-model results. The simple re-calculations report their own intervals, which are not the same analysis as the sponsor’s model.

For the high-dose re-calculated risk difference, the interval is entirely below zero. For the low-dose re-calculated risk difference, the interval includes zero. These statements describe those unadjusted re-calculations only. They do not decide the sponsor’s non-inferiority question, which requires the trial’s margin and analysis rules. A confidence interval also does not mean that the true effect has a specified probability of lying in the particular interval; in frequentist terms, the method has a long-run coverage property under its assumptions.

Why is the endpoint composite?

A composite endpoint combines several event types, here stroke and SEE. As a general statistical concept, combining outcomes can increase the number of events and may improve the ability to estimate an overall effect. However, the interpretation depends on what is included and whether components have similar clinical importance and treatment response. The registry does not report component-specific primary results, so the overall composite cannot show whether the observed pattern was driven by stroke, SEE, or both.

How should p-values be read?

A p-value summarizes how incompatible the observed data are with a specified statistical null model, conditional on the method and assumptions. It is not the probability that the null hypothesis is true, nor a measure of the size or clinical importance of an effect. The re-calculated p-values are unadjusted. The sponsor p-values belong to the reported Cox-model analyses and should be interpreted in that analysis context. The registry’s classification of an analysis as non-inferiority or equivalence does not reveal the full test specification.

Multiple outcomes and comparisons raise the possibility that some apparently notable findings occur by chance when many hypotheses are assessed. The registry lists multiple secondary outcomes and analyses, but multiplicity adjustment procedures are not reported in the registry record. Accordingly, unadjusted secondary findings are exploratory in interpretation and carry less weight than a result supported by a prespecified analysis plan and appropriate multiplicity handling.

What do the planning illustrations represent?

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. The effect to detect is the stated fraction of the observed effect. The binary-outcome figures are participants per arm; the time-to-event figures, when applicable, are total events. The primary outcome is binary, so its planning figures are participants per arm. These are planning illustrations based on posted results, not the trial’s original design calculations. The registry’s own design assumptions are not reported.

11. Confidence Intervals and Precision

The re-calculated risk differences are accompanied by confidence intervals, which show the uncertainty around those estimates under the re-calculation method. For high-dose edoxaban versus warfarin, the estimated difference is -0.010, with an interval from -0.016 to -0.004. Its endpoints are both below zero, so this simple estimate is consistent with a lower event proportion in the high-dose group. For low-dose edoxaban versus warfarin, the estimate is -0.003, with an interval from -0.009 to 0.003. That interval includes zero and spans a possible difference in either direction.

These intervals are based on unadjusted re-calculations from the posted event counts. The sponsor’s analyses use Cox proportional hazards models and report 97.5% confidence intervals: .632 to .985 for the high-dose hazard ratio of 0.79, and .874 to 1.314 for the low-dose hazard ratio of 1.07. Those model-based intervals describe a different effect measure and should not be compared as though they were intervals for risk differences.

Precision is not the same as clinical importance. A confidence interval communicates uncertainty under the chosen statistical method; it does not establish whether an effect is meaningful to patients. For non-inferiority, the interval must also be judged against a prespecified margin. That margin is not reported in the registry record, which limits independent interpretation of the sponsor’s non-inferiority classification.

Confidence intervals also do not account automatically for every source of uncertainty, such as possible bias, missing data, model misspecification, or multiplicity. The registry record does not report enough detail to assess those issues fully. The posted intervals should therefore be read as statistical precision summaries for the stated analyses, not as complete measures of certainty about all possible interpretations.

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 are planning calculations derived from the observed effect, rather than a reconstruction of the original trial design. For the binary primary endpoint, figures are participants per arm. For time-to-event planning tables, the figures are total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. Original trial design assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm, or total events for a time-to-event calculation, associated with an 80% chance of detecting the specified effect if the assumptions hold and the effect is real. The 90% power column gives the corresponding planning quantity for a higher chance of detection under those same assumptions. Greater planned power generally requires more information, which can mean more participants or more events.

Rows that use 100% of the observed effect plan around the full observed estimate. Rows using 75% or 50% of the observed effect plan around smaller effects. Smaller effects are harder to distinguish from random variation, so they require more participants or events to achieve the same target power. This is why the illustrated sample-size requirements rise as the assumed effect becomes smaller.

These figures are not observed power. They are planning illustrations that depend on the assumptions stated above and on the observed effect used as their starting point. The observed effect can be imprecise, so these calculations should not be treated as a guarantee that a future study will detect an effect or as evidence that the completed trial had a particular probability of success. The trial’s original sample-size justification and design assumptions are not reported in the registry record.

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 = 0.036; treatment proportion p₁ = 0.026; average p̄ = 0.031.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2453 = 0.4807.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2452 = 0.2063.
4. n = (0.4807 + 0.2063)² / (-0.0102)² = 4,557.9, rounded up to 4,558 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 <- 0.0361325335618395                          # control proportion
p1 <- 0.0259555048488306                          # 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(781391)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 4,558 (80% power), 6,102 (90% power)
 75% of observed effect: n per arm = 8,425 (80% power), 11,279 (90% power)
 50% of observed effect: n per arm = 19,678 (80% power), 26,343 (90% power)
power.prop.test: 4557.9 
Simulated power at n = 4,558 per arm: 0.803 (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 primary analyses are reported as Cox proportional hazards models. For high-dose edoxaban versus warfarin, the registry reports a hazard ratio of 0.79, a 97.5% confidence interval from .632 to .985, and p < .0001. For low-dose edoxaban versus warfarin, it reports a hazard ratio of 1.07, a 97.5% confidence interval from .874 to 1.314, and p = .0055. Both are classified in the registry as non-inferiority or equivalence analyses.

The re-calculated results use the posted arm counts to estimate unadjusted risk differences. They do not reproduce the sponsor’s time-to-event model, so the estimates, intervals, and p-values need not match. The registry records a discrepancy between the re-calculation and the sponsor analysis. In that circumstance, the sponsor’s own analysis takes precedence as the trial’s reported analysis.

That precedence does not make every detail of the sponsor’s inferential conclusion independently verifiable from the registry record. The non-inferiority margin, complete analysis plan, and details needed to assess model assumptions are not reported. In particular, the p-value should not be treated as a replacement for the margin-based non-inferiority decision. The posted re-calculation is useful as a transparent, unadjusted comparison of event proportions, but it answers a narrower question than the sponsor’s model-based analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists several secondary outcomes and reports multiple analyses. When many outcomes or comparisons are tested, the chance of at least one apparently notable result arising by chance can increase. Statistical methods can address this issue through a prespecified hierarchy, adjustment, or other strategy, but the registry record does not report the multiplicity procedure, if any. The interpretation of secondary p-values is consequently limited: they should not be read as independent confirmatory findings without knowing how the analyses were planned and controlled.

The primary endpoint is identified as a non-inferiority analysis. A non-inferiority conclusion depends on a prespecified margin that defines how much worse an intervention could be while still meeting the objective. That margin is not reported in the registry record. The record also does not provide the full statistical analysis plan, the rationale for the analysis population, or details of any interim analyses. Those elements should not be inferred from the reported p-values or from the analysis classification.

The primary population is described as mITT and includes randomized subjects who received one or more doses of study drug. The endpoint timeframe is on-treatment, extending to 3 days after the last dose. The registry does not give enough information to assess how missing outcome data, withdrawals, treatment discontinuation, or censoring were handled. It also does not report sensitivity analyses for the non-inferiority conclusion. These omissions matter because conclusions can depend on analysis population and assumptions about incomplete follow-up.

General statistical practice recognizes that non-inferiority analyses may require careful assessment of both intention-to-treat and per-protocol populations and of missing data, but the registry information does not state whether these were used. It would be inappropriate to assume a particular approach. The record also does not report a sample-size justification or original power assumptions. As a result, the posted sample-size illustrations should be kept separate from the trial’s design rationale, and the sponsor analyses should be interpreted with the limits of the available methodological detail in view.

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: cardiac failure (5.3%), atrial fibrillation (5.2%), cardiac failure congestive (4.2%), pneumonia (3.7%), myocardial infarction (2.7%).

The registry reports serious adverse event figures by treatment group. The reported affected counts are 3581 for warfarin/placebo edoxaban, 3393 for high-dose edoxaban/placebo warfarin, and 3448 for low-dose edoxaban/placebo warfarin. The corresponding at-risk figures are 7012, 7012, and 7002. These are descriptive safety counts, not adjusted comparisons, and the registry information does not provide confidence intervals or a statistical comparison for them.

The registry also lists other adverse-event affected counts: 4200 for warfarin/placebo edoxaban, 4201 for high-dose edoxaban/placebo warfarin, and 4057 for low-dose edoxaban/placebo warfarin. The at-risk figures are 7012, 7012, and 7002, respectively. The record does not describe the event ascertainment period or provide a comparative analysis for these counts. Death counts are not reported in the registry record.

The listed serious adverse event terms include CARDIAC FAILURE at 5.3%, ATRIAL FIBRILLATION at 5.2%, CARDIAC FAILURE CONGESTIVE at 4.2%, PNEUMONIA at 3.7%, MYOCARDIAL INFARCTION at 2.7%, and ISCHAEMIC STROKE at 2.0%. These are registry-listed terms and percentages; they should not be assumed to represent treatment-specific rates, because the record does not assign these percentages to particular arms in the available information. The counts and listed terms describe reported safety information but do not by themselves establish comparative safety.

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

The registry record describes a randomized comparison of two edoxaban regimens with warfarin for a composite of stroke and systemic embolic events during an on-treatment period. The posted event counts and unadjusted re-calculations provide a way to inspect observed event proportions. The sponsor’s Cox-model analyses provide the trial’s reported time-to-event comparisons, classified as non-inferiority or equivalence analyses. These are complementary but different statistical summaries.

The high-dose unadjusted re-calculation has a risk difference interval below zero, while the low-dose re-calculation interval includes zero. Those statements apply only to the simple count-based comparisons. The sponsor’s own analyses take precedence because the registry records a discrepancy. The available registry information does not include the non-inferiority margin or full analysis plan, so the basis for the sponsor’s non-inferiority decision cannot be independently reconstructed from these results alone.

These findings do not establish that a treatment is suitable for a particular person, and they are not medical advice. A trial-level average does not determine an individual’s outcome. The composite endpoint also does not show which component contributed to the observed event pattern; component-specific primary results are not reported in the registry record. Nor does the primary outcome alone summarize every secondary outcome or safety measure.

Interpretation is bounded by the analysis population, event definition, timeframe, and statistical methods. The primary analysis concerns randomized participants who received study drug and the on-treatment period, including up to 3 days after the last dose. The secondary outcomes use an overall-study-period timeframe. Differences in outcomes, follow-up definitions, and methods matter when comparing results. Missing-data procedures, multiplicity handling, the non-inferiority margin, and several details of the original design are not reported in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation should distinguish a posted event count from a time-to-event analysis. Counts describe how many participants experienced an event, whereas a Cox model uses event timing and follow-up under its assumptions. The resulting estimates answer related but different questions, so a count-based risk difference should not be treated as a substitute for a sponsor-reported hazard ratio.

It also illustrates the importance of the analysis framework for non-inferiority. A p-value, a hazard ratio, and a confidence interval do not by themselves define a non-inferiority conclusion; interpretation depends on the prespecified margin and analysis rules. Those details are not reported in the registry record. Recognizing the missing information prevents a reader from treating a statistical label as fully reproducible from the outcome counts alone.

The outcome is a composite, combining stroke and SEE. Composite outcomes can provide a broader endpoint and more events for analysis, but the overall estimate cannot reveal whether each component has the same pattern. Component-specific primary endpoint results are not reported in the registry record. That makes it important to keep the composite’s meaning distinct from claims about any single component.

Finally, the record shows why secondary outcomes and safety counts require context. Multiple analyses can increase the chance of findings that arise by chance, and the multiplicity plan is not reported. Descriptive adverse-event counts can inform a safety overview, but without comparative modeling, uncertainty estimates, and clear term-specific arm information, they do not provide a complete comparative safety assessment. The case demonstrates the value of reporting the analysis plan and its assumptions alongside results.

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 does not report the non-inferiority margin, the full statistical analysis plan, the original sample-size justification, or the trial’s original power assumptions. Those omissions restrict independent evaluation of the sponsor’s non-inferiority conclusions and prevent the planning illustrations from being interpreted as the trial’s design calculations.

Details on missing data, censoring, withdrawal, adherence, and sensitivity analyses are not reported in the registry record. The available information also does not describe whether model assumptions for the Cox analyses were assessed, or which covariates, if any, were included. Consequently, the reported hazard ratios cannot be fully audited from the record alone.

The primary endpoint is a composite, but component-specific primary results are not reported. The posted event counts are not accompanied by confidence intervals at the arm level, and the registry’s count-based re-calculations are unadjusted. The record indicates a discrepancy between those re-calculations and the sponsor analyses; the sponsor’s own analysis takes precedence.

The registry lists four secondary outcomes, but detailed analyses for all listed outcomes are not reported in the registry record. Multiplicity procedures are also not reported, limiting the confirmatory interpretation of secondary findings. Safety information includes group-level affected counts and a list of serious adverse event terms, but death counts are not reported, and the listed term percentages are not assigned to specific treatment groups in the available information. These limitations do not invalidate the posted results, but they define what can and cannot be inferred from the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Global Study to Assess the Safety and Effectiveness of Edoxaban (DU-176b) vs Standard Practice of Dosing With Warfarin in Patients With Atrial Fibrillation — NCT00781391.
• Registry record last updated 2019-03-05; status last verified 2015-03.
• Results first posted 2015-03-25.
• 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 describes a completed phase 3, randomized, double-blind, double-dummy, parallel-group, multi-center, multi-national study of high-dose edoxaban, low-dose edoxaban, and warfarin in participants with atrial fibrillation. Enrollment is listed as 21105. The primary endpoint was the composite of stroke and SEE in the mITT population during the on-treatment period.

The registry reports arm event counts, unadjusted re-calculations, and sponsor Cox-model analyses classified as non-inferiority or equivalence. Because a discrepancy is recorded, the sponsor’s analysis takes precedence over the simple re-calculations. The non-inferiority margin and full statistical analysis plan are not reported in the registry record. Secondary outcomes and safety counts add context, but multiplicity procedures and some outcome details are also not reported.