Phase 2 Study of the Safety, Tolerability and Pilot Efficacy of Oral Factor Xa Inhibitor Betrixaban Compared to Warfarin: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 2 Study of the Safety, Tolerability and Pilot Efficacy of Oral Factor Xa Inhibitor Betrixaban Compared to Warfarin (NCT00742859), a randomized phase 2 study. The primary outcome is Exposure-adjusted Incidence Rate of Major or Clinically Relevant Non-major Bleeding Episode.

2. Clinical Question

3. Trial Design

EXPLORE Xa (NCT00742859) was a randomized, parallel-group, phase 2, multicenter, multinational, dose-finding study. The registry records enrollment of 508 and four groups: betrixaban 40 mg, betrixaban 60 mg, betrixaban 80 mg, and warfarin. Each group’s listed outcome population is 127. The study status is completed; the recorded start was 2008-10 and primary completion was 2009-08.

The betrixaban groups received oral once-daily dosing for at least 3 months. The registry says investigators prescribed warfarin according to standard of care. The official title describes the three betrixaban doses as blinded and warfarin as open-label, while the design fields characterize masking as quadruple. These descriptions are both part of the registry record; further details about how masking was implemented are not reported in the registry record.

The primary outcome was an exposure-adjusted incidence rate of major or clinically relevant non-major bleeding, with a maximum timeframe of 1 year. The defined analysis population was all randomized patients who took at least 1 dose after randomization. The record also lists an exposure-adjusted rate for any bleeding, including major, clinically relevant non-major, or minimal bleeding. It is a phase 2 study described as assessing safety, tolerability, and pilot efficacy, rather than a record of a definitive efficacy trial.

The registry does not report the original sample-size justification or the trial’s original statistical analysis plan. Details such as stratification factors and the exact process for dose adjustment 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: 561 patients were screened for study participation. Of these patients, 508 were randomized, all of whom received at least 1 dose of study drug.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All randomized patients who took at least 1 dose of study medication after randomization.

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 patients who took at least 1 dose of study medication after randomization.

6. Primary Endpoint

The registry lists the primary outcome as Exposure-adjusted Incidence Rate of Major or Clinically Relevant Non-major Bleeding Episode, measured over A maximum of 1 year.

The primary endpoint measures the exposure-adjusted incidence rate of the first major or clinically relevant non-major bleeding episode. The registry defines the numerator as the number of subjects experiencing the event and the denominator as total person years across subjects. For a patient with an event, exposure time runs from the first dose to the first occurrence; for a patient without the event, it runs to the last study date. The result is expressed as number of patients per 100 patient years, over a maximum of 1 year.

Using exposure time accounts for differences in how long participants contribute observation. This is useful when follow-up is not identical, because a rate relates observed events to the time during which participants were at risk and under observation. The endpoint is a rate, not simply the proportion of participants who ever had an event. Its definition focuses on the first occurrence, so it does not describe the total number of repeated bleeding episodes.

The registry states that confidence intervals for this endpoint were calculated using the exact Poisson distribution. The posted group estimates and their intervals describe the precision of the rates; they do not by themselves establish that any observed difference was caused by treatment.

7. Results Posted in the Registry

• Betrixaban 60 mg: 10.10 versus 2.02 (Number of Patients per 100 Patient years) on control; rate ratio 5.00 (95% CI 0.28–89.45, derived from the posted confidence limits); p ≈ 0.274.
• Betrixaban 80 mg: 10.50 versus 2.02 (Number of Patients per 100 Patient years) on control; rate ratio 5.20 (95% CI 0.29–92.97, derived from the posted confidence limits); p ≈ 0.263.
• Warfarin: 14.60 versus 2.02 (Number of Patients per 100 Patient years) on control; rate ratio 7.23 (95% CI 0.43–122.58, derived from the posted confidence limits); p ≈ 0.171.

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.

Exposure-adjusted Incidence Rate of Any Bleeding (Major, Clinically Relevant Non-major, or Minimal)

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, with the standard error taken from the posted confidence limits.
• Result:
  • Betrixaban 60 mg: 77.90 versus 50.50 (Number of Patients per 100 Patient years) on control; rate ratio 1.54 (95% CI 0.87–2.73, derived from the posted confidence limits); p ≈ 0.136.
  • Betrixaban 80 mg: 56.00 versus 50.50 (Number of Patients per 100 Patient years) on control; rate ratio 1.11 (95% CI 0.60–2.04, derived from the posted confidence limits); p ≈ 0.740.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Betrixaban 60 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Betrixaban 80 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary outcome: the exposure-adjusted incidence rate of any bleeding, including major, clinically relevant non-major, or minimal bleeding. The posted estimates span the four treatment groups, while sponsor-reported log-rank comparisons are available for only some contrasts. Across the posted material, the secondary outcome does not yield one uniformly aligned picture across the rate-based and time-to-event summaries. The rate estimates and their uncertainty should be read together with the sponsor’s reported analyses, rather than treated as interchangeable measures.

This outcome is broader than the primary endpoint because it includes minimal bleeding as well as the more clinically significant categories. It can provide additional context about bleeding events, but it does not answer precisely the same question as the primary endpoint. Its results should not be used to override the primary analysis, especially given the different endpoint definition and analysis methods.

Secondary comparisons carry less weight when many outcomes or contrasts are examined without a reported adjustment for multiple testing. With repeated statistical tests, the chance of finding an apparently notable result by chance can increase. The registry record does not report whether a multiplicity adjustment or a prespecified hierarchy was used. The secondary findings are therefore best regarded as exploratory context, not as independent confirmation of a treatment effect.

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

• Exposure-adjusted Incidence Rate of Any Bleeding (Major, Clinically Relevant Non-major, or Minimal)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is an exposure-adjusted incidence rate. It relates the number of patients experiencing the first qualifying bleeding event to the total person-time contributed by the analysis population, and expresses the result per 100 patient years. In general, exposure adjustment can make rates more comparable when participants have different follow-up durations. It does not remove other sources of uncertainty or confounding in the analysis.

Why use an exact Poisson interval?

The registry says the confidence interval for the primary rate was calculated using the exact Poisson distribution. In general, Poisson methods are used for event counts observed over exposure time. An exact interval avoids relying on a large-sample approximation for the count distribution, which can be helpful when event counts are limited. The resulting interval represents uncertainty in the rate estimate; a broad interval means the data do not pin down the underlying rate closely. The primary intervals are broad, and the lower bound for the 40 mg group is close to zero.

What does the recalculated rate ratio represent?

The recalculated comparisons use the posted group rates to form unadjusted rate ratios, with betrixaban 40 mg as the reference. A rate ratio compares the estimated rates, not the time-to-first-event patterns of individual participants. The recalculated confidence intervals are derived from the posted summary statistics and are not the sponsor’s model-based results. For the primary comparisons, the recalculated rate ratios are 5.0 for 60 mg, 5.198 for 80 mg, and 7.228 for warfarin, each with a very wide interval. Each unadjusted p-value is 0.274, 0.263, or 0.171, respectively. These estimates should be interpreted cautiously because aggregate summaries do not preserve all the information available in participant-level time-to-event analyses.

How is a hazard ratio different?

The registry reports sponsor comparisons using log-rank methods and hazard ratios. In general, a hazard ratio compares the instantaneous event rates over follow-up, conditional on remaining event-free up to that time. It uses the timing of events and censoring, whereas a simple rate ratio compares overall exposure-adjusted rates. These are different estimands and methods, so their estimates need not agree. The registry’s reported hazard ratios are 0.14 for 40 mg versus warfarin, 0.711 for 60 mg versus warfarin, and 0.755 for 80 mg versus warfarin. The registry record does not report enough methodological detail to explain the difference between these results and the unadjusted recalculations.

Confidence intervals show a range of values compatible with the data under the stated method and assumptions. A wide interval indicates limited precision. A p-value measures how unusual data at least as incompatible with a null hypothesis would be if that hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, nor does it measure clinical importance. The sponsor-reported 40 mg interval includes the no-difference value even though its p-value is 0.035; the record does not explain this apparent inconsistency.

What do the planning illustrations mean?

The sample-size illustrations use the observed effect as a starting point and consider detecting a stated fraction of that effect. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For time-to-event calculations, the figures represent total events; for the other calculations, they represent participants per arm. These assumptions describe the illustrations, not the original trial design. The trial’s own design assumptions are not reported in the registry record.

More generally, over-dispersion occurs when variability in event counts exceeds what a simple Poisson model expects. If over-dispersion is present but not accounted for, uncertainty estimates can be too narrow. The registry record does not report an over-dispersion assessment for this outcome, so none can be inferred from the posted summaries.

11. Confidence Intervals and Precision

The 95% confidence intervals for the primary rates span a wide range. For betrixaban 40 mg, the interval is 0.05 to 11.3 patients per 100 patient years; for 60 mg, it is 3.28 to 23.6; for 80 mg, 3.41 to 24.5; and for warfarin, 5.85 to 30.0. The width of these intervals conveys that the rate estimates are not highly precise. In particular, the 40 mg estimate has a low point estimate but its interval also accommodates considerably higher rates.

The recalculated rate-ratio intervals are also very broad: 0.280 to 89.45 for 60 mg compared with 40 mg, 0.291 to 92.97 for 80 mg compared with 40 mg, and 0.426 to 122.6 for warfarin compared with 40 mg. Each includes the no-difference value. Such breadth means these recalculations do not sharply distinguish among a range of possible relative rates.

The sponsor-reported hazard-ratio intervals are broad as well. The 40 mg interval, 0.017 to 1.14, includes the no-difference value; the 60 mg interval, 0.225 to 2.24, and the 80 mg interval, 0.239 to 2.39, also include it. The sponsor-reported p-value for 40 mg is 0.035, a result that does not align straightforwardly with its posted interval. The record does not report an explanation. Precision and consistency of the reported inferential results therefore deserve attention alongside the point estimates.

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 planning figures illustrate sample sizes under stated hypothetical assumptions; they are not the number enrolled in the trial. For the primary rate comparisons, the figures are participants per arm, not total events. The planning 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 set to the stated fraction of the observed effect. For time-to-event calculations the corresponding figures would be total events, but the primary rate calculations use participants per arm.

The 80% power column means the illustrative number of participants per arm under which the calculation would have an 80% chance of detecting the specified effect, if the assumptions and effect were correct. The 90% power column expresses the same idea with a higher target chance of detection, which generally requires more participants. These are planning targets, not guarantees about a future study.

The rows compare planning around the full observed effect with planning around 75% or 50% of that effect. For example, for the warfarin comparison against betrixaban 40 mg, planning for 100% of the observed effect gives 114 participants per arm for 80% power and 152 participants per arm for 90% power. Planning for 75% gives 217 and 290 participants per arm; planning for 50% gives 546 and 730 participants per arm. The same pattern appears in the other rate comparisons: smaller effects need more participants to detect.

These calculations are planning illustrations computed from the observed effect, not the trial’s original design rationale. The original sample-size assumptions and justification are not reported in the registry record. The figures are not observed power, and they should not be read as evidence about the probability that the completed study’s findings are true.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 0.0202; treatment rate λ₁ = 0.1010 events per patient-year; follow-up T = 1.00 years.
2. n = (1.96 + 0.842)² × (1/0.0202 + 1/0.1010) / (1.00 × [ln(5.000)]²) = 180.0, rounded up to 181 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
lambda0 <- 0.0202                      # control rate, events per patient-year
lambda1 <- 0.101                      # treatment rate
tt      <- 1                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(742859)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 181 (80% power), 241 (90% power)
 75% of observed effect: n per arm = 347 (80% power), 464 (90% power)
 50% of observed effect: n per arm = 869 (80% power), 1,163 (90% power)
Simulated power, Poisson counts, n = 181 per arm: 0.898
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.685

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses for the primary endpoint using log-rank methods and hazard ratios. Those are the trial’s reported comparisons. Separate simple, unadjusted recalculations use the posted exposure-adjusted rates to form rate ratios. The methods and estimands differ, and the recalculated results do not agree with the sponsor analyses, including in direction for comparisons with betrixaban 40 mg.

The registry record flags this discrepancy. Accordingly, the sponsor’s own analysis takes precedence over the recalculation; the latter is best treated as a diagnostic comparison based on group summaries, not a replacement analysis. The sponsor-reported 40 mg hazard ratio is 0.14, with a 95% confidence interval of 0.017 to 1.14 and p = 0.035. The interval includes the no-difference value despite the reported p-value, and the registry record does not explain this tension. The sponsor-reported 60 mg and 80 mg comparisons have broad confidence intervals that include the no-difference value.

Neither priority nor precedence resolves the uncertainty in the underlying evidence. The registry does not report enough detail to reproduce the sponsor’s analysis or explain why it differs from the rate-based recalculation. The methods and the discrepancy should therefore remain visible when interpreting the results.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies the primary bleeding endpoint and one secondary bleeding endpoint, and it lists several sponsor-reported comparisons. It does not report whether statistical testing was adjusted for multiplicity, whether the comparisons followed a prespecified hierarchy, or how the primary and secondary analyses were prioritized in the original analysis plan. Without that information, the nominal p-values should not be interpreted as if the family of tests and its error control were known.

Missing-data handling is not reported in the registry record. The primary endpoint description explains how exposure time was counted for participants with and without an event, but it does not explain how missing outcome information, withdrawal, or other incomplete follow-up was handled. The registry states a maximum timeframe of 1 year; it does not provide further detail about censoring rules beyond the endpoint definition.

The defined primary analysis population is all randomized patients who took at least 1 dose of study medication after randomization. This is narrower than an analysis of every randomized participant, but the record does not report a separate intention-to-treat analysis or explain how participants who did not take a dose were handled. The arm counts shown for the primary endpoint are 127 in each group. Further detail about exclusions, protocol deviations, adherence, or analysis-population sensitivity checks is not reported in the registry record.

These omissions matter because analysis choices can affect the estimate, its uncertainty, and the interpretation of p-values. They do not establish that the analysis was conducted incorrectly; they mean that the posted record does not contain the detail needed to assess these issues fully.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 3% 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 congestive (2.4%), atrial fibrillation (0.8%), ventricular tachycardia (0.8%), angina unstable (0.8%), coronary artery disease (0.8%).

The registry lists serious adverse events for 12 participants in the betrixaban 40 mg group, 12 in the 60 mg group, 11 in the 80 mg group, and 12 in the warfarin group. Each group’s listed number at risk is 127. These are group-level counts in the registry record; they do not by themselves establish that an event was caused by the assigned treatment or describe its severity, timing, or relationship to treatment.

The most frequent serious-event term listed is congestive cardiac failure at 2.4%. Other listed terms are atrial fibrillation, ventricular tachycardia, unstable angina, coronary artery disease, and sick sinus syndrome, each at 0.8%. The registry record does not provide further event-level context in these figures. Serious adverse event counts are a safety description, not a stand-alone comparison establishing that one treatment is safer.

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

The posted data describe bleeding rates and time-to-event analyses across three betrixaban doses and warfarin in a phase 2 study of patients with non-valvular atrial fibrillation. The primary rate estimates differ across groups, but the confidence intervals are broad. The sponsor’s reported hazard-ratio analyses and simple rate-based recalculations do not agree, and the registry flags a discrepancy. The sponsor analysis takes precedence, while its reported 40 mg interval and p-value present an unresolved inconsistency.

These findings do not establish that betrixaban or warfarin prevents stroke more effectively, nor do they establish that one treatment causes more or fewer bleeding events. The primary endpoint concerns bleeding, not stroke prevention. The registry’s stated clinical context and study hypothesis are not themselves results. The listed outcomes, confidence intervals, and analyses describe what was recorded, not a definitive conclusion about efficacy or safety.

Interpretation is limited by the study’s phase 2, pilot and dose-finding context, the imprecision of the estimates, and the lack of reported detail on multiplicity, missing-data handling, and the original analysis plan. The maximum outcome timeframe was 1 year. The record does not provide the information needed to judge how well these findings generalize beyond the studied participants or to resolve the methodological discrepancy.

For clinical or research interpretation, the distinction between a point estimate and its uncertainty is essential. A rate that appears lower or higher is not, by itself, evidence of a reliable treatment difference. Here, the uncertainty and analysis discordance are central features of the posted results.

18. Why This Trial Matters Statistically

This trial offers a useful statistical example because it reports both exposure-adjusted rates and sponsor-reported time-to-event comparisons for bleeding. Those analyses answer related but not identical questions. Comparing them shows why the estimand and method matter: summary-rate recalculations need not reproduce a log-rank hazard-ratio analysis, and apparently conflicting outputs should prompt careful examination rather than selective reporting.

The primary outcome also illustrates the role of exposure time. Rates can account for differing observation time, while confidence intervals communicate how uncertain those estimates remain. In this record, the intervals are broad, so the point estimates alone would overstate the precision of the evidence. The discrepancy flag and the tension between the reported 40 mg interval and p-value further demonstrate why statistical results should be read as a set, not as isolated numbers.

Finally, the phase 2 dose-finding context makes the distinction between exploratory evidence and confirmation important. The registry offers information about bleeding outcomes and safety-event counts, but does not report key analysis-plan details, including multiplicity handling. The record is therefore valuable for learning how endpoints, estimands, uncertainty, and reporting completeness shape interpretation, without treating these data as a definitive comparative conclusion.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

Several limitations are specific to what the registry records for this study. It is described as a phase 2 dose-finding study with pilot efficacy, and the primary outcome timeframe is a maximum of 1 year. The posted outcome group counts are 127 each, and the primary rate confidence intervals are broad. This limits how precisely the event rates and comparisons can be understood from the summaries.

The registry reports a discrepancy between the simple recalculations and the sponsor’s analyses. It does not explain the source of the difference or provide enough detail to reproduce the sponsor’s model. The reported 40 mg hazard-ratio confidence interval includes the no-difference value, whereas its p-value is 0.035; the record does not reconcile those statistics. This complicates interpretation even when the sponsor analysis is given precedence.

The original statistical analysis plan, multiplicity approach, missing-data procedures, and sample-size justification are not reported in the registry record. Further details about participant characteristics, adherence, treatment discontinuation, and the handling of protocol deviations are also not reported in the registry record. The registry describes the study as quadruple-masked while the official title states that warfarin was open-label; further implementation details are not reported. These gaps restrict assessment of bias, analysis choices, and applicability beyond the population described.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Phase 2 Study of the Safety, Tolerability and Pilot Efficacy of Oral Factor Xa Inhibitor Betrixaban Compared to Warfarin — NCT00742859.
• Registry record last updated 2023-08-07; status last verified 2023-08.
• Results first posted 2017-09-26.
• 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

NCT00742859 is a completed, randomized, parallel-group phase 2 study of betrixaban and warfarin in patients with non-valvular atrial fibrillation. The registry records enrollment of 508 and four groups: betrixaban 40 mg, 60 mg, and 80 mg, and warfarin. The study’s primary outcome was the exposure-adjusted incidence rate of major or clinically relevant non-major bleeding over a maximum of 1 year.

Primary rates and sponsor-reported time-to-event comparisons are posted, along with one secondary any-bleeding outcome and serious adverse event counts. The primary estimates are imprecise, and the recalculated comparisons differ from the sponsor analyses. The registry flags this discrepancy, so the sponsor’s analyses take precedence; important details about the original statistical plan and several analysis procedures are not reported in the registry record.