Study to Gather Information About the Proper Dosing of the Oral FXIa Inhibitor BAY 2433334 and to Compare the Safety of the Study Drug to Apixaban, a Non-vitamin K Oral Anticoagulant (NOAC) in Patients With Irregular Heartbeat (Atrial Fibrillation) That Can Lead to Heart-related Complications.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Gather Information About the Proper Dosing of the Oral FXIa Inhibitor BAY 2433334 and to Compare the Safety of the Study Drug to Apixaban, a Non-vitamin K Oral Anticoagulant (NOAC) in Patients With Irregular Heartbeat (Atrial Fibrillation) That Can Lead to Heart-related Complications. (NCT04218266), a randomized phase 2 study. The primary outcome is Number of Participants With Composite of International Society on Thrombosis and Hemostasis (ISTH) Major Bleeding or Clinically Relevant Non-major (CRNM) Bleeding.

2. Clinical Question

The trial record describes a randomized, active-comparator study in people with atrial fibrillation. Its primary outcome combines major bleeding and clinically relevant non-major bleeding, so the question concerns participants experiencing either category rather than a single bleeding severity alone. Secondary outcomes include all bleeding, clinically relevant non-major bleeding, and minor bleeding.

The registry gives event counts for the asundexian 20 mg, asundexian 50 mg, pooled asundexian, and apixaban groups. The reported comparison analysis for the primary outcome is a crude incidence ratio for pooled asundexian versus apixaban. Separately, the posted recalculations express unadjusted risk differences for comparisons with the asundexian 20 mg group. These are different contrasts and should not be read as if they were the same analysis.

3. Trial Design

This is a phase 2, randomized, active-comparator-controlled, double-blind, double-dummy, parallel-group dose-finding study. The record identifies quadruple masking and reports enrollment of 755. The study is marked completed. It was sponsored by Bayer and conducted in participants with atrial fibrillation.

The study drug was BAY2433334, shown in the posted results as asundexian. Results are presented for asundexian 20 mg and asundexian 50 mg, as well as a pooled asundexian group for some comparisons. Apixaban was the active comparator. The record describes matching placebos for both drugs, consistent with the double-dummy design. For apixaban, the arm description states a usual dose of 5 mg and a reduced dose of 2.5 mg for participants meeting any 2 of the listed criteria: age 80 years or older, body weight less than 60 kg, or serum creatinine level of 1.5 mg per dL or more.

The primary outcome counts participants with ISTH major bleeding or clinically relevant non-major bleeding. Its timeframe begins after the first administration of study intervention and describes an average administration of 12 weeks, with outcome collection not starting after more than 2 days following the last administration. The primary analysis population is named as the safety analysis set.

The record also describes the study as intended to gather information about dose and safety, and to learn how the study drug moves into, through and out of the body. The original sample-size rationale, detailed statistical analysis plan, and planned interim analyses 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: 862 participants were screened. 107 participants were screening failures. 755 participants were randomized in a 1:1:1 ratio to 3 treatment groups: 251 participants to the asundexian 20 mg group, 254 participants to the asundexian 50 mg group and 250 participants to the apixaban group. 2 participants of asundexian 20 mg group never administered drug.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Safety analysis set (SAF)

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: SAF (safety analysis set)

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Composite of International Society on Thrombosis and Hemostasis (ISTH) Major Bleeding or Clinically Relevant Non-major (CRNM) Bleeding, measured over After the first administration of study intervention with an average administration of 12 weeks (but not starting after more than 2 days after the last administration).

The primary endpoint is the number of participants with a composite of ISTH major bleeding or clinically relevant non-major bleeding. Major bleeding includes fatal bleeding; symptomatic bleeding in specified critical areas or organs; overt bleeding associated with a recent hemoglobin decrease meeting the stated criterion; or overt bleeding leading to transfusion of at least the stated threshold of packed red blood cells or whole blood. Clinically relevant non-major bleeding does not meet the major-bleeding definition but involves medical intervention, hospitalization or increased level of care, or a face-to-face evaluation.

A composite endpoint combines events that share clinical relevance but can differ in severity. It can capture more events than a narrowly defined component alone, while its overall count does not reveal how many events arose from each component unless those component results are separately reported. The record posts some secondary component outcomes, but a composite result should not be interpreted as a result for every individual type of bleeding.

The registry describes assessment after the first study administration, with an average administration of 12 weeks and a specified allowance after the last administration. This short-term safety outcome is suited to describing bleeding events observed during the recorded treatment and follow-up window. It does not, by itself, describe longer-term risks or establish comparative safety beyond that window.

7. Results Posted in the Registry

• Asundexian 50 mg: 0.4% (1/254) versus 1.2% (3/249) on control; risk difference -0.8 percentage points (95% CI -2.4 to 0.7), risk ratio 0.33 (0.03–3.12); unadjusted two-proportion z-test p = 0.306.
• Asundexian Pooled: 0.8% (4/503) versus 1.2% (3/249) on control; risk difference -0.4 percentage points (95% CI -2.0 to 1.2), risk ratio 0.66 (0.15–2.93); unadjusted two-proportion z-test p = 0.582.
• Apixaban: 2.4% (6/250) versus 1.2% (3/249) on control; risk difference 1.2 percentage points (95% CI -1.1 to 3.5), risk ratio 1.99 (0.50–7.88); unadjusted two-proportion z-test p = 0.316.

8. Secondary Efficacy Endpoints

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

Number of Participants With All Bleeding

• 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:
  • Asundexian 50 mg: 3.9% (10/254) versus 4.8% (12/249) on control; risk difference -0.9 percentage points (95% CI -4.5 to 2.7), risk ratio 0.82 (0.36–1.86); unadjusted two-proportion z-test p = 0.629.
  • Asundexian Pooled: 4.4% (22/503) versus 4.8% (12/249) on control; risk difference -0.4 percentage points (95% CI -3.7 to 2.8), risk ratio 0.91 (0.46–1.80); unadjusted two-proportion z-test p = 0.782.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Asundexian 50 mg 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 Asundexian Pooled and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants of ISTH Clinically Relevant Non-major (CRNM) Bleeding

• 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:
  • Asundexian 50 mg: 0.4% (1/254) versus 1.2% (3/249) on control; risk difference -0.8 percentage points (95% CI -2.4 to 0.7), risk ratio 0.33 (0.03–3.12); unadjusted two-proportion z-test p = 0.306.
  • Asundexian Pooled: 0.8% (4/503) versus 1.2% (3/249) on control; risk difference -0.4 percentage points (95% CI -2.0 to 1.2), risk ratio 0.66 (0.15–2.93); unadjusted two-proportion z-test p = 0.582.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Asundexian 50 mg 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 Asundexian Pooled and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With ISTH Minor Bleeding

• 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:
  • Asundexian 50 mg: 3.5% (9/254) versus 4.0% (10/249) on control; risk difference -0.5 percentage points (95% CI -3.8 to 2.9), risk ratio 0.88 (0.36–2.13); unadjusted two-proportion z-test p = 0.781.
  • Asundexian Pooled: 3.8% (19/503) versus 4.0% (10/249) on control; risk difference -0.2 percentage points (95% CI -3.2 to 2.7), risk ratio 0.94 (0.44–1.99); unadjusted two-proportion z-test p = 0.873.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Asundexian 50 mg 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 Asundexian Pooled and the control. The interval gives the range of effects that remain compatible with the data.

The secondary bleeding outcomes broadly show the same interpretive challenge as the primary result: the posted counts are modest, and the comparisons are uncertain. The secondary endpoints cover all bleeding, clinically relevant non-major bleeding, and minor bleeding. The registry also posts crude incidence ratios for pooled asundexian versus apixaban for these outcomes, with 90% intervals.

Across these outcomes, the point estimates and reported analyses should be read alongside their intervals, not as definitive rankings. The endpoints overlap conceptually with the primary composite: the primary combines major bleeding with clinically relevant non-major bleeding, while secondary measures broaden or separate aspects of bleeding. They therefore add descriptive context, but they are not independent confirmation of the primary result.

The secondary analyses are unadjusted in the posted recalculations, and the registry record does not report a multiplicity strategy. When several outcomes and comparisons are examined, the chance of encountering an apparently notable result by chance can increase. Without a stated hierarchy or adjustment, secondary p-values and intervals generally carry less confirmatory weight than a prespecified primary analysis. The registry does not report enough detail to establish how the secondary outcomes were prioritized in the original analysis plan.

The appropriate overall reading is descriptive: the secondary results show the pattern of reported bleeding counts and comparisons during the study window, but they do not remove the uncertainty around the primary endpoint or establish a definitive treatment difference.

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

• Number of Participants With All Bleeding
• Number of Participants With ISTH Major Bleeding
• Number of Participants of ISTH Clinically Relevant Non-major (CRNM) Bleeding
• Number of Participants With ISTH Minor Bleeding

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: the record counts whether a participant experienced the composite bleeding outcome. A count of participants with an event is different from an event rate per unit of follow-up time. The registry-reported primary analysis is called a crude incidence ratio, while the posted recalculations use risk differences. These measures answer related but distinct questions.

What does a risk difference describe?

A risk difference compares the observed proportions with an event in two groups by subtracting one group’s proportion from the other. It is an absolute contrast, expressed on the proportion scale. A negative estimate in these comparisons means the event proportion in the named comparison arm is lower than in the asundexian 20 mg reference group under the posted calculation; a positive estimate means it is higher. The estimate does not adjust for covariates unless an adjusted method is specified. The posted recalculations are described as simple, unadjusted calculations from summary statistics.

How does an incidence ratio differ?

An incidence ratio is relative rather than absolute: it compares incidence between groups. The registry lists a crude incidence ratio for pooled asundexian versus apixaban. Because the registry record does not give a p-value or further methodological details for that analysis, the ratio should be described as reported rather than reverse-engineered into another test. A relative measure can look different in scale from an absolute difference, and the two estimates are not interchangeable.

What does a confidence interval add?

A confidence interval conveys uncertainty around an estimate. A narrow interval indicates greater precision than a wide interval, while an interval spanning the no-difference value indicates that the data do not clearly separate effects in opposite directions under that calculation. This is not a statement that all values in the interval are equally likely, nor does it establish that the true effect is exactly the point estimate. The confidence level for the recalculated intervals is not reported in the registry record. The registry-reported incidence-ratio interval is explicitly described as 90%.

Why do sparse events matter?

When only a small number of participants experience an outcome, moving a small number of observations can substantially affect the estimated contrast. Sparse data commonly produce broad uncertainty intervals. The main issue is precision: the point estimate can be unstable, and the data may be compatible with a range of effects. It is therefore important to consider event counts and intervals together rather than treating a single estimate or p-value as a complete summary.

What do the p-values say?

The recalculated p-values are unadjusted and relate to the specified risk-difference comparisons. A p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the test; it is not the probability that a treatment is effective or ineffective. The registry record does not report multiplicity adjustment for these analyses. When many endpoints or contrasts are examined, unadjusted p-values can overstate the strength of evidence if interpreted as though only one comparison had been planned.

What is the role of the posted recalculation?

Recalculation from aggregate counts provides a transparent, unadjusted contrast that readers can compare across arms. It cannot reproduce a more detailed sponsor analysis that may use a different estimand, exposure-time handling, adjustment, or analysis population unless those details are available. Here the registry-reported primary analysis is a crude incidence ratio for pooled asundexian versus apixaban, whereas the recalculated measures use risk differences against asundexian 20 mg. The difference in comparison and measure matters when interpreting apparent agreement or disagreement.

The record names the safety analysis set for the primary endpoint. Details about how missing outcome data were handled, whether participants were analyzed according to randomized assignment, and the exact analysis model are not reported in the registry record. General statistical interpretation must therefore remain limited to the posted counts, estimates, and stated methods.

11. Confidence Intervals and Precision

The primary outcome has few observed events in each listed arm: 3 in asundexian 20 mg, 1 in asundexian 50 mg, 4 in pooled asundexian, and 6 in apixaban. With sparse events, estimates are especially sensitive to individual outcomes, and uncertainty is substantial relative to the point estimates.

For the recalculated comparison of asundexian 50 mg with asundexian 20 mg, the risk difference is -0.008 and its interval runs from -0.024 to 0.007. For pooled asundexian versus asundexian 20 mg, the estimate is -0.004 with an interval from -0.020 to 0.011. For apixaban versus asundexian 20 mg, the estimate is 0.012 with an interval from -0.011 to 0.035. All three intervals include no difference and encompass values in both directions. Thus, the point estimates alone do not support a precise ranking of the groups.

The registry-reported pooled-asundexian versus apixaban crude incidence ratio is 0.33, with a 90% confidence interval from 0.09 to 0.97. This interval is broad on the ratio scale. It is a separate sponsor-reported analysis and not the same contrast as the recalculated risk differences. The confidence level for those recalculated intervals is not reported in the registry record, so it should not be inferred from the displayed bounds.

Intervals are useful because they put the estimate in context: they show the range of effects not ruled out by the data under the analysis. They do not establish equivalence, prove no difference, or resolve clinically meaningful thresholds. The registry record does not report a prespecified equivalence or non-inferiority margin for this endpoint.

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 figures are planning illustrations based on the observed effect, not the trial's original design assumptions. The stated calculation uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row scales the effect to detect to the stated fraction of the observed effect.

For these binary participant-count outcomes, the figures are participants per arm, not total events. The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and model assumptions were correct. The 90% power column gives the corresponding planning target for a higher chance of detection. These are prospective design quantities; they are not a measure of what the completed trial achieved.

The rows for 100%, 75%, and 50% of the observed effect let readers see how the illustrative requirement changes if the effect of interest is smaller than the observed estimate. Smaller effects need more participants to distinguish them from no difference under the same assumptions. Where an observed effect is very small, the resulting planning figures can become very large. Such outputs should be read as sensitivity illustrations, not as a recommended design for a future study.

This is not observed power. The original trial's sample-size justification and design assumptions are not reported in the registry record. The posted planning values also rely on an effect estimated from this study, so they should not be treated as independent confirmation of that effect or as evidence that the study was adequately or inadequately powered.

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 = 0.012; treatment proportion p₁ = 0.004; average p̄ = 0.008.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1259 = 0.2468.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1258 = 0.1059.
4. n = (0.2468 + 0.1059)² / (-0.0081)² = 1,890.6, rounded up to 1,891 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 <- 0.0120481927710843                          # control proportion
p1 <- 0.00393700787401575                          # 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(4218266)
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 = 1,891 (80% power), 2,531 (90% power)
 75% of observed effect: n per arm = 3,785 (80% power), 5,067 (90% power)
 50% of observed effect: n per arm = 9,467 (80% power), 12,673 (90% power)
power.prop.test: 1890.6 
Simulated power at n = 1,891 per arm: 0.826 (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 registry-reported primary analysis compares pooled asundexian with apixaban and gives a crude incidence ratio of 0.33, with a 90% confidence interval from 0.09 to 0.97. No p-value is listed for that analysis. This result is distinct from the unadjusted recalculations, which express risk differences and compare each listed arm with asundexian 20 mg.

For the pooled group, the recalculated risk difference against asundexian 20 mg is -0.004, with an interval from -0.020 to 0.011. The two analyses differ in both contrast and measure: pooled asundexian versus apixaban for the reported incidence ratio, versus pooled asundexian versus asundexian 20 mg for the recalculated absolute difference. Their estimates should not be expected to match numerically.

The posted recalculation is a simple unadjusted analysis from summary counts and does not replace the registry-reported analysis. The record does not provide enough detail to reconstruct the sponsor's full method or determine how its incidence ratio was calculated. Because the discrepancy flag is false, no discrepancy is identified between the posted data and the registry analysis; the sponsor's reported analysis remains the relevant registry result for its stated comparison.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary composite endpoint and several secondary bleeding outcomes. It also presents multiple treatment contrasts, including dose-specific and pooled asundexian comparisons. Examining several outcomes and contrasts raises a multiplicity question: if each is tested separately without adjustment or a prespecified testing sequence, the chance of at least one apparently unusual result may be higher than for a single planned test.

The registry record does not report whether the original statistical plan used a multiplicity adjustment, a hierarchical testing procedure, or another way to control interpretation across endpoints. It also does not report a detailed analysis hierarchy. The recalculated p-values are unadjusted, so they should not be interpreted as multiplicity-controlled confirmatory evidence. The reported incidence-ratio analyses do not list p-values.

The primary endpoint identifies the safety analysis set as its population. The record does not report the full inclusion rules for that set, whether analyses followed randomized assignment, or how participants with missing outcome information were handled. It does not state whether missing outcomes were imputed, treated as no event, or addressed using another method. Those details matter because missingness can affect both event counts and comparisons.

The record also does not report the detailed statistical model, any covariate adjustments, interim-analysis procedures, or the original sample-size justification. These omissions do not invalidate the posted counts, but they limit assessment of how the original sponsor analysis was specified and whether all relevant design decisions are visible. The recalculated summaries should therefore be understood as unadjusted analyses of posted aggregate data, not as a reconstruction of the complete analysis plan.

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 0% 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 (1.6%), atrial fibrillation (1.2%), cerebrovascular accident (0.8%), palpitations (0.4%), sinus arrest (0.4%).

The adverse-event record lists serious adverse events affecting 20 participants in the asundexian 50 mg group, 22 in the asundexian 20 mg group, and 20 in the apixaban group. It separately lists other adverse events affecting 116, 110, and 113 participants in those respective groups. Deaths are listed as 4, 2, and 5, respectively. These are descriptive counts; they do not establish that an event was caused by study treatment.

The most frequent serious-event terms listed include cardiac failure at 1.6%, atrial fibrillation at 1.2%, and cerebrovascular accident at 0.8%; palpitations, sinus arrest, and congestive cardiomyopathy are each listed at 0.4%. These term percentages describe the registry's adverse-event reporting and should not be confused with the primary bleeding endpoint.

Adverse-event summaries require attention to definitions, exposure duration, severity, and attribution. The record does not provide the full event-level context needed to infer comparative causality from these counts. A count difference alone is not a treatment-effect estimate, particularly without a stated adjusted analysis or uncertainty interval.

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

The results describe observed bleeding counts and posted comparisons in a randomized phase 2 study of asundexian and apixaban among participants with atrial fibrillation. They offer short-term safety information for the recorded treatment and follow-up period and include a dose-finding purpose. They do not establish a definitive comparative safety conclusion from the primary endpoint.

The primary event counts are small, and the recalculated risk-difference intervals include no difference. That means the posted unadjusted comparisons are imprecise; it does not mean the treatments are equivalent, nor does it prove that there is no difference. The registry-reported pooled-asundexian versus apixaban incidence ratio is a different analysis and comparison, and should be interpreted with its reported 90% interval rather than conflated with the recalculations.

The data also do not establish the optimal asundexian dose. The record describes dose finding, but does not report a dose-selection rule or a formal conclusion identifying a best dose. Nor do the short-term bleeding outcomes establish long-term risks, benefits, or effects on stroke or other heart-related outcomes. Although the study description discusses the rationale for anticoagulant treatment, those outcomes are not the primary endpoint analyzed.

Finally, the posted results do not provide the full original statistical plan, missing-data approach, or multiplicity strategy. Those omissions constrain interpretation of the sponsor's analysis and of secondary outcomes. The sound conclusion is limited to what is directly reported: event counts, the specified comparisons, and the uncertainty attached to them.

18. Why This Trial Matters Statistically

This trial is statistically instructive because it combines a dose-finding question with an active safety comparison and reports a composite bleeding endpoint. The study design includes randomization, masking, and an active comparator, while the results illustrate how a formal design can still yield substantial uncertainty when the primary outcome is uncommon.

It also shows why the estimand and comparison need to be explicit. The registry-reported crude incidence ratio compares pooled asundexian with apixaban, whereas the unadjusted recalculations compare each arm with asundexian 20 mg using risk differences. A relative incidence measure and an absolute proportion difference answer different questions. Quoting an estimate without naming its comparator and scale can make unlike analyses appear to conflict.

The study is a useful example of the distinction between event counts and precision. Low counts can produce wide intervals, so a point estimate should not be treated as a settled ranking. The secondary outcomes add breadth but also raise multiplicity concerns; without a reported adjustment or testing hierarchy, they are most safely read as supporting descriptive evidence.

Finally, planning illustrations based on observed effects show how strongly sample-size requirements can depend on the effect chosen for detection. These calculations are not the original design rationale and are not observed power. Keeping planning assumptions separate from observed evidence is essential when interpreting a completed study.

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 primary endpoint counts participants with a composite event, and the observed counts are sparse. That limits precision and makes estimates sensitive to a small number of outcomes. The endpoint also combines major and clinically relevant non-major bleeding, which differ in severity; the composite count alone does not describe the clinical profile of each event.

The registry-reported primary analysis and posted recalculations use different comparisons and measures. The former is a crude incidence ratio for pooled asundexian versus apixaban; the recalculations are unadjusted risk differences against asundexian 20 mg. The registry record does not provide enough methodological detail to reproduce the sponsor analysis or align its estimand exactly with the recalculations.

The reported timeframe describes an average administration of 12 weeks and a follow-up allowance after the last administration. It therefore cannot support conclusions about longer-term outcomes. The registry record does not report the original sample-size justification, detailed statistical analysis plan, interim analyses, multiplicity approach, missing-data handling, or complete analysis-population rules beyond naming the safety analysis set for the primary endpoint.

The secondary endpoints involve multiple outcomes and contrasts, with no multiplicity strategy reported. The registry's adverse-event counts are also descriptive and do not by themselves show causality. These limitations call for restrained interpretation: the posted information characterizes outcomes observed in this study but leaves important questions about analysis choices and broader generalizability unresolved.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Gather Information About the Proper Dosing of the Oral FXIa Inhibitor BAY 2433334 and to Compare the Safety of the Study Drug to Apixaban, a Non-vitamin K Oral Anticoagulant (NOAC) in Patients With Irregular Heartbeat (Atrial Fibrillation) That Can Lead to Heart-related Complications. — NCT04218266.
• Registry record last updated 2022-10-27; status last verified 2022-10.
• Results first posted 2022-10-27.
• 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, randomized, quadruple-masked, parallel-group phase 2 study sponsored by Bayer, with enrollment of 755 participants with atrial fibrillation. It compared asundexian at 20 mg and 50 mg with apixaban and included a pooled asundexian presentation.

The primary outcome was the number of participants with ISTH major or clinically relevant non-major bleeding during the stated treatment and follow-up window. The registry reports a crude incidence ratio for pooled asundexian versus apixaban; unadjusted recalculations provide risk differences against asundexian 20 mg. The primary event counts are low and the recalculated intervals include no difference. The results should be read as imprecise short-term safety findings, not as proof of equivalence or a definitive dose ranking.

Details of the original sample-size justification, missing-data methods, multiplicity strategy, and full statistical plan are not reported in the registry record.