Apixaban for Early Prevention of Recurrent Embolic Stroke and Hemorrhagic Transformation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Apixaban for Early Prevention of Recurrent Embolic Stroke and Hemorrhagic Transformation (NCT02283294), a randomized phase 3 study. The primary outcome is Number of Participants With a Composite Endpoint of Fatal Stroke, Recurrent Ischemic Stroke, or TIA.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group phase 3 trial comparing apixaban with warfarin. Masking is recorded as none, so the design was open label. The registry lists an enrollment of 91 and a completed study. The posted primary-outcome groups contain 41 participants for apixaban and 47 for warfarin. The registry record does not explain the distinction between its enrollment figure and the posted endpoint group counts.

The treatment schedules differed in their planned timing of initiation. Apixaban was described as twice daily for 180 days, with initiation timing varying according to whether the participant had a transient ischemic attack, small stroke, or medium stroke. Warfarin was described as standard of care, with its own start times based on event category. This comparison therefore concerns the assigned treatment strategies as recorded, including their distinct start-time descriptions; it is not simply a comparison of the two drug names independent of timing.

The registry lists the University of South Florida as sponsor. The recorded study start was 2015-04 and the primary completion was 2019-06. The title and brief summary describe an interest in early prevention of another stroke and hemorrhagic transformation, while the posted primary endpoint is a composite of fatal stroke, recurrent ischemic stroke, or transient ischemic attack. Intracranial hemorrhage assessed by MRI/CT is listed as a secondary outcome.

Further details about eligibility criteria, recruitment sites, sequence generation, allocation concealment, protocol deviations, and the trial's own sample-size justification are not reported in the registry record. The reported analysis count is 0, and no reported analyses are listed. Thus, the available registry results support a descriptive reading of the posted group outcomes and comparisons, but do not give a full account of the trial's analysis procedures.

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: Ninety one patients were enrolled/consented into the study. Three patients of the 91 consented did not meet one or more of the inclusion/exclusion criteria and were excluded prior to randomization assignment.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With a Composite Endpoint of Fatal Stroke, Recurrent Ischemic Stroke, or TIA, measured over 180 days.

The primary endpoint counts participants with a composite of fatal stroke, recurrent ischemic stroke, or transient ischemic attack during 180 days. It is a binary outcome at the participant level: a participant either had an event meeting the composite definition during the specified period or did not. The registry reports counts of participants, rather than the number of total events, so multiple events in one participant are not represented as separate endpoint counts in these results.

A composite endpoint can capture several clinically relevant event types within one outcome and can make an overall comparison possible when each component is uncommon. Its interpretation depends on knowing which events qualify and whether the components differ in importance or frequency. In this record, the component definitions beyond the named events and the component-specific results are not reported in the registry record. The combined result therefore cannot show whether any particular component accounts for the observed group counts.

The endpoint is assessed over 180 days, making the time window part of its meaning. The posted count is not a time-to-event estimate and does not indicate when events occurred within that period. The comparison should be read as a difference in the proportion of participants with the composite outcome, as estimated in the posted results, rather than as a direct measure of event timing or severity.

7. Results Posted in the Registry

• Warfarin: 25.5% (12/47) versus 17.1% (7/41) on control; risk difference 8.5 percentage points (95% CI -8.5 to 25.4), risk ratio 1.50 (0.65–3.44); unadjusted two-proportion z-test p = 0.336.

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 an Intracranial Hemorrhage Assessed by MRI/CT

• 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:
  • Warfarin: 12.8% (6/47) versus 12.2% (5/41) on control; risk difference 0.6 percentage points (95% CI -13.3 to 14.4), risk ratio 1.05 (0.34–3.18); unadjusted two-proportion z-test p = 0.936.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Warfarin and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists one secondary outcome: participants with an intracranial hemorrhage assessed by MRI/CT during 180 days. The posted counts and comparison are available alongside the primary outcome. At a broad level, the secondary result does not supply a precise counterweight that resolves the uncertainty in the primary comparison. Both outcomes are based on relatively small groups, and their estimates should be read with their confidence intervals rather than as definitive evidence for a difference or no difference.

The secondary endpoint is related to the study's stated interest in hemorrhagic transformation and safety, while the primary endpoint addresses a composite of recurrent ischemic and transient ischemic events and fatal stroke. These outcomes concern different event definitions. A result for one cannot stand in for the other, and a combined reading does not reveal a detailed balance between each individual benefit- or harm-related event. The registry does not report more granular timing or participant-level relationships between the endpoints.

Unadjusted secondary results generally carry less evidential weight than a clearly prespecified primary comparison because examining additional outcomes creates more opportunities for apparently notable findings. Without a reported multiplicity plan, the nominal uncertainty measures for secondary outcomes do not account for the broader set of possible comparisons. The registry does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes.

The record lists 0 reported analyses and no reported analyses for the secondary endpoint. Consequently, the posted summary comparison is not accompanied by detail about the intended model, analysis population, or missing data. The secondary finding is best treated as descriptive context for the primary result, not as independent confirmation or a definitive safety conclusion. The registry's limited outcome detail also means that no inference should be made about unlisted secondary endpoints or unreported event categories.

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

• Number of Participants With an Intracranial Hemorrhage Assessed by MRI/CT

9. Statistical Interpretation

10. Statistical Methods Explained

The registry results concern a binary participant-level endpoint and a comparison between two randomized groups. The statistics need to be interpreted in light of the endpoint definition, the size of the groups, and the limitations of the analysis information available in the registry record.

What does a risk difference represent?

A risk difference compares the proportions of participants with an event in two groups by subtracting one group’s event proportion from the other. The comparison is labeled as warfarin relative to apixaban. A positive estimate therefore indicates a higher observed event proportion in the warfarin group; a negative estimate indicates a higher observed proportion in the apixaban group. The risk-difference estimate is 0.085. It is a measure of absolute contrast, rather than a relative measure such as a ratio.

Absolute contrasts are often useful because they express how far apart the two group event proportions are on the probability scale. Their interpretation still depends on the endpoint and follow-up period. In this trial the outcome is a composite measured over 180 days, and the registry reports participants with an event rather than recurrent event counts. The risk difference does not describe event severity, timing, or which composite component occurred.

How should the confidence interval be read?

A confidence interval describes the uncertainty around an estimated quantity under the assumptions of the method used. In repeated use of a procedure, intervals constructed in the same way would cover the underlying quantity at the stated confidence level at the corresponding long-run rate. It is not a range that assigns a probability to the true effect after the data have been observed. The interval for the primary risk difference extends from -0.085 to 0.254. Its breadth indicates that the posted results leave substantial uncertainty about the size and direction of the difference.

When an interval for a risk difference includes no difference, it is compatible with no separation between the group proportions as well as with contrasts in either direction. This does not prove equality. A wide interval can reflect limited information, including a small number of participants or outcome events; it means that more than one materially different underlying contrast remains compatible with the posted data.

What does the p-value add?

The unadjusted p-value of 0.336 is a tail probability calculated under a no-difference model and the assumptions of the test. It is not a measure of effect size and does not tell whether the estimated contrast is clinically important. It also does not distinguish between inadequate information and a genuinely small effect. Because the registry does not provide the trial's own complete analysis plan, the posted p-value should be treated as an unadjusted comparison rather than assumed to represent every planned statistical decision.

General statistical interpretation: a p-value is conditional on a model and on the analysis being performed. It does not account automatically for multiple endpoints, repeated analyses, missing data, or departures from the analysis plan. Those issues require information about the planned and performed analyses, which is not reported in the registry record.

Why might over-dispersion matter?

General statistical explanation: over-dispersion arises when observed variability is greater than a model expects. It can make standard errors too small if the model assumes less variability than the data contain, leading to intervals that are too narrow and p-values that are too optimistic. This issue is especially relevant for some count models. The primary outcome is reported as the number of participants with a binary event, not as an event-rate count model, and the registry does not report an over-dispersion assessment or a model-based analysis. It would therefore be inappropriate to infer that such an adjustment was or was not used beyond what the registry records.

What can be concluded from the analysis record?

The registry lists no reported analyses. It provides group counts and comparison statistics, but does not report the named test, covariate adjustment, analysis population, handling of missing endpoint data, or model diagnostics. These omissions limit the ability to reconstruct the analysis or assess whether all design features were reflected in it. The comparisons can still be described as posted unadjusted estimates, but they do not replace a full statistical analysis plan or detailed trial report.

The same basic caution applies to the secondary endpoint. Its outcome is also a participant count over 180 days, and the registry gives a comparison, but the record does not document a multiplicity strategy. A nominal result for an additional endpoint should not be interpreted as if it were the sole prespecified test unless the analysis plan supports that interpretation. More broadly, estimates and p-values are informative only alongside their definitions, uncertainty, and the design and analysis decisions that generated them.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.085, with a 95% confidence interval from -0.085 to 0.254. The interval is wide enough to include contrasts on either side of no difference. It therefore conveys more than the point estimate alone: the data are compatible with a range of possible group differences, and the direction is not determined precisely by the posted observations.

Precision is constrained by the amount of outcome information. The posted primary groups contain 41 participants assigned to apixaban and 47 assigned to warfarin, with 7 and 12 participants, respectively, counted with the composite outcome. In a binary endpoint, the information about a contrast depends on both group sizes and event counts. A small trial can yield a point estimate that appears substantial while still leaving a broad interval around it.

The confidence interval is not a statement that every value within its limits is equally plausible, nor that values outside it are impossible. It summarizes sampling uncertainty under the statistical procedure and its assumptions. The registry does not report enough detail to assess all those assumptions or determine whether the interval was generated by the trial's prespecified method.

Precision should also be distinguished from bias and relevance. A narrow interval would indicate greater statistical precision, but would not by itself rule out bias, outcome misclassification, or limits in applicability. Conversely, a broad interval does not show that the underlying difference is absent; it shows that this record does not estimate it tightly. The absence of component-specific primary results adds another kind of uncertainty: the overall composite cannot identify which event types contribute to the observed contrast.

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 are participants per arm for the binary outcomes, not total event counts. They are illustrations based on the observed effect, not the original design justification for the trial. The registry record states the planning assumptions: a two-sided significance level of 0.05, equal allocation between the arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The trial's own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true effect and the calculation's model were appropriate. The 90% power column uses the same idea but targets a 90% chance. Power is a design-stage probability conditional on assumptions; it is not a measure of the probability that the trial's conclusion is correct.

Rows using 100%, 75%, and 50% of the observed effect represent progressively smaller effects to detect. Smaller differences are harder to distinguish from sampling variation, so the planning calculation requires more participants per arm as the effect becomes smaller. The results are sensitive to the observed effect used as the starting point, which is uncertain in a small study. In particular, planning figures derived from a noisy estimate should not be treated as dependable forecasts of the sample size needed to answer a future question.

These numbers are not observed power. Observed power is not a useful substitute for reading the estimate and its confidence interval, and the planning calculations do not explain why the trial enrolled the number it did. They are statistical illustrations under the stated assumptions, rather than evidence that the study had a particular intended target or was designed around the effects shown.

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 = 0.171; treatment proportion p₁ = 0.255; average p̄ = 0.213.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5790 = 1.1349.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5759 = 0.4847.
4. n = (1.1349 + 0.4847)² / (0.0846)² = 366.6, rounded up to 367 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 <- 0.170731707317073                          # control proportion
p1 <- 0.25531914893617                          # 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(2283294)
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 = 367 (80% power), 491 (90% power)
 75% of observed effect: n per arm = 629 (80% power), 842 (90% power)
 50% of observed effect: n per arm = 1,360 (80% power), 1,820 (90% power)
power.prop.test: 366.6 
Simulated power at n = 367 per arm: 0.801 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns arise when several outcomes, comparisons, subgroups, or analysis choices are examined. Each additional opportunity to identify a result can increase the chance of observing an apparently unusual finding even when no underlying difference exists. Statistical approaches can address this, for example by adjusting thresholds or defining an ordered testing strategy, but the appropriate method depends on the planned questions and analysis design.

The registry lists a primary composite endpoint and one secondary endpoint, and reports no analyses. A multiplicity strategy, endpoint hierarchy, or adjustment procedure is not reported in the registry record. This means the posted unadjusted results should not be treated as though multiplicity was controlled, and no claim can be made that a particular adjustment was intended or omitted in the trial's full analysis.

Missing-data handling is also not reported in the registry record. The posted primary group counts are 41 and 47, while registry enrollment is 91; the record does not explain that distinction. It does not specify whether all randomized participants were included in the endpoint analysis, how unavailable endpoint assessments were treated, whether participants were censored or excluded, or whether sensitivity analyses were conducted. These details matter because an analysis that excludes participants with missing outcome information can differ from one that makes explicit assumptions about their outcomes.

The analysis populations are not described. In randomized trials, intention-to-treat, per-protocol, and safety populations can include different sets of participants and answer different questions. General explanation: intention-to-treat analysis usually retains participants according to randomized assignment, while per-protocol analysis focuses on adherence to specified treatment procedures. The registry does not identify which population generated the posted results, so it is not appropriate to assign either label to these estimates.

The record also does not report a prespecified statistical analysis plan, interim analyses, covariate adjustment, or sensitivity analyses. Their presence or absence cannot be inferred from the posted group statistics. These omissions do not establish that the trial was improperly analyzed; they mean that the registry record alone does not allow readers to evaluate those aspects of the analysis.

15. 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: recurrent stroke (14.9%), fatal stroke (6.4%), worsening congestive heart failure (4.9%), third degree av block (4.3%), worsening atrial fibrillation (4.3%).

The registry reports serious adverse events affecting 11 of 41 participants in the apixaban group and 14 of 47 in the warfarin group. It also reports other adverse events affecting 36 of 41 and 41 of 47, respectively. These are participant counts in the recorded groups. They should be read as descriptive safety summaries, not as adjusted comparisons or proof that an event was caused by treatment.

The record lists 2 deaths for apixaban and 4 for warfarin. It does not provide enough detail in these figures to establish the timing, cause, or treatment attribution of each death. Serious-event terms listed include recurrent stroke at 14.9%, fatal stroke at 6.4%, worsening congestive heart failure at 4.9%, third degree AV block at 4.3%, worsening atrial fibrillation at 4.3%, and TIA at 4.3%. The registry does not give arm-specific attribution for these listed percentages in the adverse-event summary.

The counts do not show how many participants experienced multiple distinct adverse events, and the registry record does not report event-level timing or severity detail beyond the serious-event classification. Differences between group counts should not be treated as causal estimates without the corresponding analysis and uncertainty information.

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

The primary result describes the participants with a composite event during 180 days in the two randomized groups. The point estimate is higher for warfarin relative to apixaban, but the confidence interval is broad and includes differences in either direction. The result therefore does not establish a precise underlying contrast, and the unadjusted p-value does not resolve that uncertainty.

The result does not show that apixaban prevents stroke, nor does it show that it fails to do so. It also does not establish that the treatments are equivalent. A failure to obtain a precise distinction is not evidence that two strategies have identical effects. The posted data are compatible with multiple possible underlying differences, including differences that could be important in either direction; the registry record alone does not determine which is true.

The composite endpoint combines fatal stroke, recurrent ischemic stroke, and transient ischemic attack. Since the registry does not give separate counts for these components, the overall comparison cannot identify which component drove the group totals. It is also not a time-to-event analysis, so it does not establish when outcomes occurred. The outcome is not a complete measure of all potential benefits or harms of the treatment strategies.

The trial's timing schedules are part of the interventions described. Any interpretation pertains to the randomized strategies as recorded, not to a general comparison of apixaban and warfarin across all clinical circumstances or initiation schedules. The registry provides limited information on participant characteristics, adherence, missing outcomes, and analysis populations, so generalization beyond the enrolled participants and the recorded treatment schedules is constrained.

These observations are statistical findings, not a basis for an individual treatment decision. The trial's completed status and phase label do not eliminate the uncertainty in its posted results. A fuller interpretation would require more detail about the protocol, analysis plan, participant flow, outcome components, and complete trial reporting, none of which can be reconstructed from the posted summary alone.

17. Why This Trial Matters Statistically

This trial illustrates why an estimate should be read together with its uncertainty. The direction of the primary point estimate can appear straightforward, but the confidence interval indicates that the posted results leave substantial room for different underlying contrasts. Treating the point estimate alone as a settled answer would ignore the limited information in the observed groups.

It also shows how the definition of an endpoint affects the question being answered. The composite combines fatal stroke, recurrent ischemic stroke, and transient ischemic attack. A single summary can be useful, but without component-specific results it cannot establish whether the components behave similarly or which one contributes most to the group comparison. The secondary intracranial hemorrhage outcome addresses a distinct aspect of the study question and should not be conflated with the primary composite.

The planning illustrations show the consequence of targeting smaller effects: more participants are needed under the stated calculation assumptions. They also highlight the caution required when an observed effect from a small study is used as the planning basis. Such calculations are not the same as the trial's original design rationale, which is not reported in the registry record, and they do not describe the trial's achieved probability of detecting an effect.

Finally, the record demonstrates the limits of registry summaries for statistical appraisal. The randomized design is important, but the registry does not report key analysis details, including the analysis populations, missing-data procedures, or multiplicity plan. Statistical interpretation depends not only on a test statistic but also on the prespecified question and how the data were analyzed. Recognizing what is and is not documented is part of reading trial evidence responsibly.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary endpoint is a composite, but the registry does not report the counts for fatal stroke, recurrent ischemic stroke, and transient ischemic attack separately. It is therefore not possible to tell whether the overall group counts reflect a consistent pattern across components or are concentrated in one component. Nor does the record provide timing of events within the 180-day follow-up window.

The registry enrollment is 91, while the posted primary groups contain 41 and 47 participants. The record does not explain the difference or provide a participant flow account. Without information on randomization, exclusions, endpoint availability, and analysis populations, it is difficult to determine how the posted outcome groups relate to all enrolled participants.

The design is recorded as open label. The registry does not describe masking of outcome assessors or whether endpoint adjudication was independent. This matters as a limitation of what can be evaluated from the registry, but the record does not establish whether such procedures were or were not used. Likewise, adherence, treatment changes, and the handling of protocol deviations are not reported.

The registry does not provide detailed eligibility criteria or participant characteristics. That limits assessment of how closely the enrolled group represents other populations with atrial fibrillation after transient ischemic attack or stroke. The treatment schedules also vary by event category, but the record does not give subgroup outcomes by category or detailed information about how those schedules were implemented.

Finally, no full statistical analysis plan, analysis-population definition, missing-data approach, or multiplicity strategy is reported. The posted estimates are consequently difficult to evaluate against prespecified procedures. These record-specific gaps limit interpretation; they do not by themselves demonstrate that the underlying trial lacked procedures or that the posted results are incorrect.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Apixaban for Early Prevention of Recurrent Embolic Stroke and Hemorrhagic Transformation — NCT02283294.
• Registry record last updated 2021-11-30; status last verified 2018-12.
• Results first posted 2021-11-30.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry identifies a completed randomized, open-label, parallel-group phase 3 trial sponsored by the University of South Florida. It compared apixaban, described as twice daily for 180 days with initiation timing based on event category, with warfarin described as standard of care with different start times.

The primary outcome was the number of participants with fatal stroke, recurrent ischemic stroke, or transient ischemic attack during 180 days. The posted primary groups report 7 participants with the composite among 41 assigned to apixaban and 12 among 47 assigned to warfarin. The risk-difference estimate is 0.085, with a 95% confidence interval from -0.085 to 0.254 and an unadjusted p-value of 0.336.

One secondary outcome, intracranial hemorrhage assessed by MRI/CT, is listed. The registry record does not report a full analysis plan, analysis populations, missing-data methods, or multiplicity handling. The posted primary comparison is imprecise and does not establish a definitive direction or magnitude of difference.