Study to Gather Information About the Proper Dosing and Safety of the Oral FXIa Inhibitor BAY 2433334 in Patients Following an Acute Heart Attack: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Gather Information About the Proper Dosing and Safety of the Oral FXIa Inhibitor BAY 2433334 in Patients Following an Acute Heart Attack (NCT04304534), a randomized phase 2 study. The primary outcome is Efficacy - Number of Participants With Composite of CV Death, MI, Stroke and Stent Thrombosis (ST).

2. Clinical Question

The trial question is dose-finding as well as comparative: three doses were evaluated against placebo in people following an acute myocardial infarction. The registry describes a randomized, placebo-controlled, double-blind study in its official title and lists quadruple masking in its design fields. The summary says BAY 2433334 blocks a step in blood clotting and was evaluated alongside dual antiplatelet therapy. The posted results describe the composite endpoint and several individual cardiovascular outcomes, but do not establish which component, if any, accounts for the overall count pattern. The endpoint definitions and the low observed event counts matter when interpreting the comparisons: they limit the precision with which differences between assigned groups can be assessed.

3. Trial Design

The registry record describes a phase 2, randomized, parallel-group, placebo-controlled, double-blind study in its official title. Its design fields list quadruple masking and randomized allocation. It identifies Bayer as sponsor and records an enrollment of 1601. The record is marked completed. The study began on 2020-06-17, and primary completion is recorded as 2022-02-21. Those dates describe the registry record and do not by themselves explain the duration of follow-up for every participant.

Four arms are listed: asundexian 10 mg, asundexian 20 mg, asundexian 50 mg and placebo. The arm counts for the primary outcome are 397, 401, 402 and 401, respectively. The study summary describes treatment after a recent myocardial infarction and use on top of dual antiplatelet therapy, stated as acetylsalicylic acid with or without clopidogrel. Specific eligibility criteria, treatment duration, dose schedule, adherence procedures and detailed background-treatment rules are not reported in the registry record.

The primary endpoint is recorded from baseline up to 52 weeks and counts participants with a composite of cardiovascular death, myocardial infarction, stroke or stent thrombosis. The endpoint population is labelled FAS, but the registry record does not define that population. The study has eight named secondary outcomes and ten outcome measures in total; fifteen analyses are listed in the record. These counts describe what is posted, not a full statistical analysis plan. Planned hypotheses, the intended hierarchy among outcomes and the original sample-size justification are not reported in the registry record.

The groups and treatment allocation support comparisons of each dose with placebo. However, the registry record does not report details such as randomization strata, concealment procedures or the exact roles of the masking categories. The posted sponsor analyses include Cox proportional-hazards results for selected group comparisons, while the primary outcome is also represented by event counts. These approaches address related but not identical summaries: event counts describe whether participants had events during follow-up, while a time-to-event analysis incorporates when events occurred.

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: 1664 participants were screened, 63 participants were screening failures. 1601 participants were randomized in a 1:1:1:1 ratio to 4 treatment groups: 397, 401, and 402 participants to the asundexian 10 mg, 20 mg and 50 mg groups and 401 participants to the placebo group

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS

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: FAS(Full data analysis)

6. Primary Endpoint

The registry lists the primary outcome as Efficacy - Number of Participants With Composite of CV Death, MI, Stroke and Stent Thrombosis (ST), measured over From baseline up to 52 weeks.

The primary endpoint counts participants with at least one event in a composite of cardiovascular death, myocardial infarction, stroke or stent thrombosis from baseline up to 52 weeks. The registry defines cardiovascular death to include death due to stroke, myocardial infarction, heart failure or cardiogenic shock, sudden death and other cardiovascular causes; death due to non-traumatic hemorrhage is included. Myocardial infarction requires evidence of myocardial necrosis in a clinical setting consistent with acute myocardial ischemia. Stroke is defined as an acute episode of focal or global neurological dysfunction caused by brain, spinal cord or retinal injury resulting from hemorrhage or infarction. Stent thrombosis includes definite cases confirmed angiographically or pathologically, and probable cases meeting the described relationship to myocardial infarction and ischemia in the stent territory without another obvious cause.

A composite is used to combine several clinically important event types into one outcome. In general, combining events can capture more participants with an outcome than evaluating each component separately and can support an overall comparison when individual components are uncommon. It also means the composite count does not reveal which component drives the pattern. Components may differ in frequency and clinical importance, so the total should not be read as if it represented one uniform event.

The registry reports counts of participants, not the number of recurrent events or a severity-weighted score. It also lists a time-to-event analysis separately. The endpoint definition gives the event window, but additional rules about adjudication, handling of multiple components, and treatment of participants with incomplete follow-up are not reported in the registry record.

7. Results Posted in the Registry

• Asundexian 10 mg: 6.8% (27/397) versus 5.5% (22/401) on control; risk difference 1.3 percentage points (95% CI -2.0 to 4.6), risk ratio 1.24 (0.72–2.14); unadjusted two-proportion z-test p = 0.439.
• Asundexian 20 mg: 6.0% (24/401) versus 5.5% (22/401) on control; risk difference 0.5 percentage points (95% CI -2.7 to 3.7), risk ratio 1.09 (0.62–1.91); unadjusted two-proportion z-test p = 0.761.
• Asundexian 50 mg: 5.5% (22/402) versus 5.5% (22/401) on control; risk difference -0.0 percentage points (95% CI -3.2 to 3.1), risk ratio 1.00 (0.56–1.77); unadjusted two-proportion z-test p = 0.993.

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.

Efficacy - Number of Participants With CV Death

• 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 10 mg: 1.8% (7/397) versus 0.5% (2/401) on control; risk difference 1.3 percentage points (95% CI -0.2 to 2.7), risk ratio 3.54 (0.74–16.91); unadjusted two-proportion z-test p = 0.091.
  • Asundexian 20 mg: 1.0% (4/401) versus 0.5% (2/401) on control; risk difference 0.5 percentage points (95% CI -0.7 to 1.7), risk ratio 2.00 (0.37–10.86); unadjusted two-proportion z-test p = 0.412.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Asundexian 10 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 20 mg and the control. The interval gives the range of effects that remain compatible with the data.

Efficacy - Number of Participants With MI

• 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 10 mg: 4.5% (18/397) versus 4.2% (17/401) on control; risk difference 0.3 percentage points (95% CI -2.5 to 3.1), risk ratio 1.07 (0.56–2.04); unadjusted two-proportion z-test p = 0.839.
  • Asundexian 20 mg: 5.0% (20/401) versus 4.2% (17/401) on control; risk difference 0.7 percentage points (95% CI -2.2 to 3.7), risk ratio 1.18 (0.63–2.21); unadjusted two-proportion z-test p = 0.614.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Asundexian 10 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 20 mg and the control. The interval gives the range of effects that remain compatible with the data.

Efficacy - Number of Participants With Stroke

• 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 10 mg: 1.0% (4/397) versus 0.5% (2/401) on control; risk difference 0.5 percentage points (95% CI -0.7 to 1.7), risk ratio 2.02 (0.37–10.97); unadjusted two-proportion z-test p = 0.405.
  • Asundexian 20 mg: 0.7% (3/401) versus 0.5% (2/401) on control; risk difference 0.2 percentage points (95% CI -0.8 to 1.3), risk ratio 1.50 (0.25–8.93); unadjusted two-proportion z-test p = 0.654.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Asundexian 10 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 20 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover cardiovascular death, myocardial infarction, stroke, stent thrombosis, all-cause mortality and several bleeding definitions. The posted counts for cardiovascular death, myocardial infarction and stroke are low across the arms. Their overall pattern does not make the primary composite result more certain: individual outcomes contain fewer events than the combined endpoint and therefore offer limited precision on their own.

These outcomes help describe which event categories contributed to the clinical questions being studied, but they should not be treated as independent confirmation of the primary result. Secondary analyses typically involve multiple comparisons, and the chance of at least one apparently unusual result can increase when many outcomes or dose comparisons are examined. The registry record does not report a multiplicity adjustment, a formal hierarchy for testing outcomes or a prespecified strategy for interpreting secondary p-values. Any unadjusted secondary results therefore carry less inferential weight than a result supported by a prespecified, multiplicity-controlled analysis.

Secondary counts can also be difficult to compare because outcome definitions and event frequencies differ. A sparse count is not strong evidence that an outcome is absent, and variation across small counts can occur by chance. The composite primary endpoint combines several event types, while the secondary measures separate selected components or describe mortality and bleeding. As a result, secondary outcomes are useful context but do not by themselves explain the composite comparison.

The posted results should be read as exploratory descriptions unless the registry record documents a confirmatory testing strategy. No additional interpretation of the secondary results as establishing a treatment benefit or harm is warranted from these summaries alone.

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

• Efficacy - Number of Participants With CV Death
• Efficacy - Number of Participants With MI
• Efficacy - Number of Participants With Stroke
• Efficacy - Number of Participants With Stent Thrombosis
• Efficacy - Number of Participants With All Cause Mortality
• Safety - Number of Participants With All Bleeding
• Safety - Number of Participants With BARC Bleeding Definition Type 3, 5
• Safety - Number of Participants With BARC Bleeding Definition Type 1,2,3,5

9. Statistical Interpretation

10. Statistical Methods Explained

What is being compared? The primary outcome is a binary participant-level result: whether a participant had at least one component of the composite during the recorded follow-up window. The arm counts and group sizes allow an unadjusted comparison of observed event risks between each asundexian dose and placebo. In general, a risk difference expresses the difference between two event probabilities; a value of zero represents no difference in those risks. This is distinct from a hazard ratio, which compares event rates over time under a time-to-event model.

The recalculated comparisons are explicitly unadjusted. They use posted summary counts and group sizes rather than participant-level data or a fitted covariate-adjusted model. An unadjusted comparison does not account for any baseline variables or study design features unless those are already incorporated in the posted summary. The registry record does not report enough detail to establish whether the posted summary counts reflect every planned analytic rule, such as censoring, imputation or a specific estimand.

How should the p-values be read? A p-value describes how compatible the observed data are with a specified statistical model under a null hypothesis, in this case a no-difference comparison for the recalculated risk difference. In general, a small p-value can indicate that the data would be unusual under that null model, but it does not measure the probability that the null is true, the size of an effect or its clinical importance. The recalculated p-values are unadjusted and should not be treated as controlling the chance of false-positive findings across the multiple endpoints and comparisons.

What does a confidence interval convey? In general, a confidence interval gives a range of values compatible with the observed data and the method's assumptions at its stated confidence level. For a risk difference, a range that includes zero indicates that no difference is among the values compatible with the data at that level. It does not mean every value in the range is equally likely, nor does it guarantee that the true value lies within that particular interval. The primary recalculations include zero in each interval, and the reported ranges are broad enough that materially different effects cannot be distinguished with precision.

Why is a time-to-event model also reported? A count-based risk comparison treats participants as having or not having an event over the outcome window. A Cox proportional-hazards analysis uses the timing of events and, ordinarily, accounts for differing follow-up through risk sets and censoring. The reported sponsor analysis is labelled Cox proportional hazard and uses log-rank methods for the primary outcome analyses. In general, a hazard ratio is a relative comparison of event hazards over time, not a risk difference and not a direct comparison of final event proportions. Its interpretation depends on model assumptions, including proportional hazards. The registry record does not provide diagnostics or other information that would allow assessment of that assumption.

The sponsor's posted Cox results carry 90% confidence intervals. The recalculated binary comparisons use risk differences and report their confidence intervals and unadjusted p-values. Because the metrics and analysis methods differ, their numerical estimates should not be compared as if they were interchangeable. Both sets of results address the groups' outcomes, but one summarizes event counts and the other models event timing.

What does low event frequency imply? In general, when outcomes are uncommon, a small number of events can strongly influence the estimated difference. The uncertainty in an estimate often remains substantial even when the total number of participants is sizeable, because precision depends importantly on how many outcome events occur. This study's primary counts range from 22 to 27 across the four arms. The broad reported time-to-event intervals and risk-difference intervals reflect limited precision, rather than establishing that effects are exactly absent.

What can the registry record establish about the analysis plan? It identifies the primary outcome, the outcome window and some sponsor-reported analyses. It does not report the original sample-size justification, interim-analysis plan, multiplicity strategy, missing-data approach, detailed model specification or the definition of FAS. Those omissions prevent a full reconstruction of the planned analysis. General statistical explanations above describe what the methods mean; they do not imply that unreported procedures were or were not used.

11. Confidence Intervals and Precision

Precision is limited by the number of primary events. The posted counts are 27 for asundexian 10 mg, 24 for 20 mg, 22 for 50 mg and 22 for placebo. Although the arm sizes are around 400 participants each, the comparisons are informed by relatively few participants with the composite outcome. With few events, estimates can change noticeably with a small change in the event count, and confidence intervals tend to be wide.

The recalculated risk-difference confidence intervals include zero for all three dose-versus-placebo comparisons. For the sponsor-reported Cox analyses, the 90% confidence intervals also include the no-difference value of 1. The interval for the reported 20 mg versus placebo comparison runs from 0.674 to 1.781; for 50 mg versus placebo it runs from 0.614 to 1.656. The grouped comparison involving 20 mg, 50 mg and placebo has a 90% interval from 0.687 to 1.612. These ranges permit uncertainty in either direction and do not tightly pin down the size of a difference.

A confidence interval is not a range of observed participant outcomes. In general, it is an uncertainty range for an estimated effect under the assumptions of the statistical method. A wide interval signals that the data are compatible with a broad range of effect sizes. Its inclusion of no difference does not prove that there is no effect; likewise, an estimate near no difference does not guarantee that large differences are ruled out if the interval remains wide.

The sponsor analyses use 90% confidence intervals, whereas confidence intervals for the recalculated risk differences are listed as ranges without a confidence level in the available record. These should not be compared as though they were necessarily constructed at the same confidence level. In particular, precision should be judged from the interval's span and the method that produced it, not from whether a p-value crosses a threshold.

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 effects, not the original design calculations. For the binary outcomes in this analysis, figures are participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The original trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column represents the number of participants per arm that the planning calculation estimates would be needed to detect the selected effect with 80% power under those assumptions. The 90% column uses a higher target probability of detecting that effect, if it is present, and therefore generally requires more participants per arm. These are planning quantities, not observed outcomes and not evidence about the power achieved by this trial.

Rows for 100%, 75% and 50% of the observed effect illustrate how the calculation changes when the target effect is made smaller. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm to detect them at the same target power. In some comparisons, the observed effect is very close to zero, producing extremely large planning figures. Such results should be read as a sign that the observed contrast is a weak basis for estimating the sample size needed to detect a smaller effect, not as a recommendation for a future trial.

These calculations are illustrative rather than a reconstruction of the phase 2 trial's design. They do not incorporate an unreported multiplicity adjustment, attrition assumption, covariate strategy or time-to-event design assumption. They are not observed power: observed power is not a useful substitute for reading the effect estimate and its uncertainty after a trial has ended.

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 = 0.055; treatment proportion p₁ = 0.068; average p̄ = 0.061.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3396 = 0.6656.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3395 = 0.2857.
4. n = (0.6656 + 0.2857)² / (0.0131)² = 5,235.5, rounded up to 5,236 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 <- 0.0548628428927681                          # control proportion
p1 <- 0.0680100755667506                          # 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(4304534)
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 = 5,236 (80% power), 7,009 (90% power)
 75% of observed effect: n per arm = 9,076 (80% power), 12,149 (90% power)
 50% of observed effect: n per arm = 19,895 (80% power), 26,633 (90% power)
power.prop.test: 5235.5 
Simulated power at n = 5,236 per arm: 0.802 (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-reported analyses use Cox proportional-hazards models and log-rank methods for the primary endpoint, and report hazard ratios with 90% confidence intervals. The recalculated comparisons use the posted participant counts and group sizes to estimate unadjusted risk differences, confidence intervals and p-values. The methods answer related but distinct questions: the recalculation contrasts event proportions, while the sponsor analysis uses event timing.

For 20 mg versus placebo, the reported Cox estimate is 1.096, with a 90% confidence interval from 0.674 to 1.781 and p = 0.756. For 50 mg versus placebo, it is 1.008, with a 90% confidence interval from 0.614 to 1.656 and p = 0.978. The additional reported comparison involving 20 mg, 50 mg and placebo has an estimate of 1.052, with a 90% confidence interval from 0.687 to 1.612 and p = 0.844. The registry record does not list a sponsor-reported Cox comparison of 10 mg versus placebo.

The sponsor results and the unadjusted recalculations both indicate considerable uncertainty; their estimates should not be treated as duplicate calculations because their estimands and methods differ. The registry record indicates no discrepancy between its posted analysis and the recalculation. The Cox outputs remain the sponsor's own reported analyses, while the risk-difference results are simple unadjusted recalculations from the posted summary statistics.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary composite outcome, multiple secondary outcomes and multiple dose-versus-placebo comparisons. Evaluating several outcomes and comparisons creates a multiplicity issue: in general, the more statistical tests performed, the greater the chance that at least one result may appear notable by chance alone. Whether and how that risk was controlled matters when interpreting secondary p-values and any collection of nominal comparisons.

A multiplicity strategy, such as a testing hierarchy or a specified adjustment, is not reported in the registry record. The posted recalculated p-values are explicitly unadjusted. The record does not establish whether the sponsor used a formal multiplicity procedure for the reported analyses. Accordingly, the unadjusted comparisons should not be interpreted as if they controlled the family-wise chance of false-positive findings across doses, outcomes and analyses.

The registry identifies the primary endpoint population as FAS but does not define its membership or describe how participants with missing outcome information were handled. Missing-data rules, censoring details for the time-to-event analyses and the analysis population for each secondary outcome are not reported in the registry record. It is therefore not possible from these entries to determine whether every randomized participant contributed to every analysis, or how incomplete follow-up may have affected the estimates.

The record also does not report interim analyses, stopping rules, model diagnostics, covariate adjustment plans or the original sample-size justification. These details can affect how evidence is evaluated, but their absence from the registry record is not evidence that a particular procedure was or was not used. The posted results support interpretation of the stated counts and reported analyses, while important parts of the full analysis plan remain unavailable in the registry record.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: acute myocardial infarction (2.5%), covid-19 (1.7%), angina pectoris (1.5%), chest pain (1.3%), cardiac failure (1.3%).

The safety summary lists serious adverse events and other adverse events by group, alongside the number at risk. Serious adverse events affected 74 of 395 participants in the 10 mg group, 82 of 397 in the 20 mg group, 67 of 402 in the 50 mg group and 82 of 399 in the placebo group. Other adverse events affected 89 of 395, 118 of 397, 94 of 402 and 107 of 399 participants, respectively. The recorded death counts are 10, 7, 10 and 7 in those groups.

These are descriptive counts from the registry record. They do not, by themselves, establish that an event was caused by the assigned treatment or that observed differences between groups are statistically reliable. The record's leading serious-event terms include acute myocardial infarction at 2.5%, COVID-19 at 1.7%, angina pectoris at 1.5%, chest pain at 1.3%, cardiac failure at 1.3% and unstable angina at 1.0%. The safety summary does not provide enough context to infer comparative causal risks for individual terms.

Safety findings should be interpreted with attention to definitions, follow-up, exposure and the number of participants assessed. Further details about attribution, severity, treatment discontinuation and exposure-adjusted analyses are not reported in the registry record.

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

The posted results describe a randomized comparison of three asundexian doses with placebo after acute myocardial infarction. For the primary composite outcome, the event counts are similar across the four arms, and the recalculated risk-difference confidence intervals include no difference. The sponsor-reported time-to-event estimates also have broad 90% confidence intervals that include the no-difference value. Taken together, these findings indicate that the available comparisons do not precisely distinguish the groups on the primary outcome.

That interpretation is narrower than saying the treatments are the same. Lack of a statistically clear difference does not demonstrate equivalence, non-inferiority or absence of a clinically relevant effect. The estimates remain compatible with a range of effects, and the relatively few primary events limit precision. Conversely, a numerical difference in counts does not establish a real treatment effect when the uncertainty is broad.

The primary endpoint combines cardiovascular death, myocardial infarction, stroke and stent thrombosis. The overall count cannot show whether any one component drove the result, and component-specific outcomes are also sparse. Secondary comparisons add descriptive context but involve multiple outcomes, with no multiplicity strategy reported in the registry record. Safety counts are likewise descriptive and should not be treated as proof of causation.

The study is a phase 2 dose-finding trial and the posted data concern the recorded population and follow-up. They do not establish how results would generalize beyond that setting. The registry record does not report the detailed eligibility criteria, full analysis plan or definition of the FAS population, which constrains interpretation of who contributed to the primary analysis and how all planned decisions were made.

The most defensible statistical reading is that the posted event counts and analyses leave substantial uncertainty around comparisons with placebo. They neither establish a clear difference nor rule out important differences. No medical decision should be inferred from these statistical summaries alone.

18. Why This Trial Matters Statistically

This study illustrates a common challenge in clinical biostatistics: a large enrollment does not automatically yield a precise estimate for an uncommon outcome. The primary composite was recorded in relatively few participants in each arm, so the amount of information about comparative effects is constrained by the number of events as well as by the number enrolled. The broad intervals make that limitation visible.

It also shows why the estimand matters. A count-based risk difference summarizes whether participants had an event over the follow-up window, whereas a Cox model uses the timing of events. These methods can produce results that are related but not numerically interchangeable. Clear interpretation requires naming the effect measure, its confidence interval and the assumptions that accompany it, rather than relying on a single p-value.

The dose-finding context is another important feature. There are three active doses and a placebo group, multiple secondary outcomes and more than one type of analysis. Without a reported multiplicity strategy and complete analysis plan, secondary results warrant particular caution. Separating prespecified primary inference from exploratory patterns is important when many comparisons are available.

Finally, the sample-size illustrations show how difficult it can be to plan around small observed contrasts, especially when those estimates are themselves uncertain. Planning calculations can help describe the scale of a future study under explicit assumptions, but they cannot replace a design justification or turn the outcome of a completed trial into observed power. This case underscores the value of transparent reporting of populations, missing-data rules, testing strategies and model assumptions alongside numerical 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.

Several limitations are specific to the information recorded for this study. The primary endpoint has relatively few events in each arm, leaving the comparisons imprecise. The composite combines cardiovascular death, myocardial infarction, stroke and stent thrombosis, which are distinct outcomes; the total count alone does not show the contribution of each component. The secondary outcomes are also sparse, limiting what can be learned from individual comparisons.

The registry labels the primary population FAS but does not define that population. It does not describe missing-data handling, censoring details, outcome adjudication procedures beyond the endpoint definitions, or the analysis population used for each outcome. Detailed eligibility criteria and the original sample-size justification are also not reported in the registry record. These omissions limit independent assessment of representativeness, follow-up completeness and consistency between planned and posted analyses.

The sponsor-reported Cox analyses cover selected comparisons; a 10 mg versus placebo Cox result is not reported in the posted analyses. The record does not report model diagnostics, proportional-hazards assessment or a full model specification. The recalculated risk differences are unadjusted and based on summary counts, so they cannot reflect covariate adjustment or participant-level analysis choices that are not available in the record.

Multiplicity procedures, interim analyses, stopping rules and a complete statistical analysis plan are not reported in the registry record. As a result, secondary findings and collections of comparisons should not be treated as confirmatory absent further documentation. Safety figures are counts and listed terms; details needed to assess exposure, attribution and comparative causal risk are not reported.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Gather Information About the Proper Dosing and Safety of the Oral FXIa Inhibitor BAY 2433334 in Patients Following an Acute Heart Attack — NCT04304534.
• Registry record last updated 2023-04-05; status last verified 2023-04.
• Results first posted 2023-04-05.
• 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 record describes a completed phase 2 randomized, parallel-group, placebo-controlled study of BAY 2433334, listed in the arms as asundexian, after acute myocardial infarction. The four groups received 10 mg, 20 mg, 50 mg or placebo. Enrollment is recorded as 1601, and the primary outcome counts participants with cardiovascular death, myocardial infarction, stroke or stent thrombosis from baseline up to 52 weeks.

Primary event counts were 27, 24, 22 and 22 across the 10 mg, 20 mg, 50 mg and placebo groups, respectively. The recalculated risk-difference comparisons and sponsor-reported time-to-event analyses show substantial uncertainty. The registry also posts secondary outcome counts and descriptive safety figures. Definitions of the FAS population, missing-data procedures, multiplicity strategy and original sample-size justification are not reported in the registry record.