Rivaroxaban Versus Warfarin in Acute Ischemic Stroke With Atrial Fibrillation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Rivaroxaban Versus Warfarin in Acute Ischemic Stroke With Atrial Fibrillation (NCT02042534), a randomized phase 2 study. The primary outcome is Number of Participants With Intracranial Bleeding and/or Recurrent Ischemic Lesion as Confirmed by MRI Imaging.

2. Clinical Question

The question reflects a clinical trade-off described in the registry rationale. Early recurrence after an ischemic stroke associated with atrial fibrillation is a concern, while anticoagulation in the acute stage raises concern about intracranial bleeding. The rationale states that aspirin has limited efficacy for preventing recurrent stroke in atrial fibrillation and that expert consensus suggests early anticoagulation in non-severe stroke with atrial fibrillation. It also describes limitations of warfarin, including delayed action and the possibility of prolonged hospitalization while waiting for full anticoagulation.

The trial therefore set out to compare an early rivaroxaban strategy with a warfarin strategy on an imaging-based combined endpoint, alongside separate outcomes such as hospitalization and recurrent ischemic lesions. This is a comparison of the regimens as described in the registry, in the population and time period studied; it does not by itself establish how the strategies would perform in other settings or populations.

3. Trial Design

The registry describes a randomized, parallel-group, phase 2 trial with no masking. The sponsor is Asan Medical Center, and the official title describes a conceptual multicenter trial. Enrollment is listed as 195. The study began in 2014-01, had primary completion in 2015-12, and is marked completed. The registry record does not report the original sample-size justification or detailed design assumptions.

The two treatment groups were rivaroxaban and warfarin. Rivaroxaban was intended to start within 5 days from stroke onset. The regimen description specifies an initial period of rivaroxaban 10mg QD after randomization, followed by 20mg QD, or 15mg in case of Cr CL. The warfarin strategy included aspirin 100mg until the INR value exceeded 1.7, then warfarin alone with a target INR value of 2.5 [2.0 - 3.0]. These descriptions matter when interpreting the comparison: the warfarin group initially received aspirin as well as warfarin.

The primary endpoint was assessed 1 month after randomization. It combined intracranial bleeding and recurrent ischemic lesion, with the registry defining the components through symptoms and follow-up imaging. Other registered outcomes included intracranial bleeding, recurrent ischemic lesion, length of hospitalization, and modified Rankin Score of 0 or 1 at Week 4. Results are posted for three secondary outcomes in the available information; a result for the modified Rankin outcome is not reported in the registry record.

No masking was used, according to the design information. The registry record does not report details of allocation concealment, site-level enrollment, adherence, treatment discontinuation, interim analyses, or the statistical analysis plan. These omissions limit what can be concluded about implementation and prespecified analysis choices. The study is marked completed, but the registry record alone does not provide a basis for judging whether every planned analysis or follow-up procedure was completed as intended.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: * modified Intention to treat: 95 / 88 (Rivaroxaban/Warfarin) * Per protocol: 93 / 87 (Rivaroxaban/Warfarin) * Safety: 98 / 90 (Rivaroxaban/Warfarin)

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: Modified Intention-to-treat analysis : The subject who is measured for the primary end point with IP is administered more than at least once after randomization

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Intracranial Bleeding and/or Recurrent Ischemic Lesion as Confirmed by MRI Imaging, measured over 1 month after randomization.

The primary endpoint counts participants with intracranial bleeding and/or a recurrent ischemic lesion, confirmed by MRI imaging, 1 month after randomization. It is a composite endpoint: a participant qualifies through either of the two specified types of event. Intracranial bleeding includes symptomatic hemorrhage confirmed by CT or MRI and asymptomatic hemorrhage on follow-up GRE or SWI imaging at 1 month. Recurrent ischemic lesion includes symptomatic ischemic stroke confirmed by relevant neuroimaging or an asymptomatic recurrent ischemic lesion on follow-up or FLAIR imaging at 1 month.

A combined endpoint can capture more than one clinically relevant concern in a single outcome, which may be useful when the treatment strategy is intended to balance bleeding risk against recurrent ischemia. That is a general statistical rationale, not evidence that the components are equally important or have the same consequences. A composite result also needs to be interpreted alongside its components: the overall count does not show, by itself, which component contributes most or whether the components move in the same direction.

The registry separately lists intracranial bleeding and recurrent ischemic lesion as secondary outcomes, which helps readers examine those components individually. The endpoint is based on whether a participant experienced an event, not on event severity or the number of events. The registry description does not report a severity-weighted measure for the composite.

7. Results Posted in the Registry

• Warfarin: 54.5% (48/88) versus 49.5% (47/95) on control; risk difference 5.1 percentage points (95% CI -9.4 to 19.5), risk ratio 1.10 (0.83–1.46); unadjusted two-proportion z-test p = 0.493.

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.

The Number of Patients With Intracranial 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:
  • Warfarin: 28.4% (25/88) versus 31.6% (30/95) on control; risk difference -3.2 percentage points (95% CI -16.4 to 10.1), risk ratio 0.90 (0.58–1.40); unadjusted two-proportion z-test p = 0.640.
• 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 Number of Patients With Recurrent Ischemic Lesion

• 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: 35.2% (31/88) versus 28.6% (28/98) on control; risk difference 6.7 percentage points (95% CI -6.7 to 20.1), risk ratio 1.23 (0.81–1.88); unadjusted two-proportion z-test p = 0.330.
• 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.

Length of Hospitalization

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Warfarin: mean 5.60 versus 4.60 on control; difference 1.00 (95% CI -0.20 to 2.20), standardized effect d = 0.24; z-test p = 0.101.
• 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 secondary outcomes broaden the picture beyond the primary composite: the registry lists intracranial bleeding, recurrent ischemic lesion, length of hospitalization, and modified Rankin Score of 0 or 1 at Week 4. Results are posted for the first three. A result for modified Rankin Score of 0 or 1 at Week 4 is not reported in the registry record.

At an overall level, the secondary outcomes do not eliminate the uncertainty surrounding the primary composite. The component outcomes help readers consider whether the combined endpoint may conceal differing patterns across bleeding and recurrent ischemia, while hospitalization addresses a separate aspect of care. The fact that these outcomes are related to the trial rationale does not make them interchangeable with the primary endpoint. Each has its own definition, follow-up information, and statistical comparison.

Secondary outcomes are often useful for understanding the breadth and consistency of findings, but they may be less reliable as stand-alone evidence. If several outcomes are tested, the chance of at least one apparently notable result can increase unless the analysis plan addresses multiplicity. No multiplicity adjustment or hierarchy among secondary endpoints is reported in the registry record. Their results therefore merit cautious interpretation and should not be treated as confirmatory simply because a p-value is small.

In particular, the hospitalization analyses use different approaches: the recalculated mean comparison and the reported rank-based test are not identical tests of the same quantity. That difference is a reason to examine methods and summaries together, rather than selecting a result solely by whether its p-value crosses a conventional threshold. The secondary findings can inform questions for further study, but they do not establish a definitive overall advantage for either treatment strategy.

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

• The Number of Patients With Intracranial Bleeding
• The Number of Patients With Recurrent Ischemic Lesion
• Length of Hospitalization
• Number of Participants With Modified Rankin Score of 0 or 1 at Week 4

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary comparison estimate?

The posted primary comparison uses a risk difference, which contrasts the proportion of participants with the endpoint in one group against the proportion in the other. In the registry’s ordering, the warfarin proportion is 0.545 and the rivaroxaban proportion is 0.495, and the risk difference is 0.051. A risk difference is an absolute contrast on the probability scale. It is not the same measure as a risk ratio or an odds ratio, which express relative contrasts in different ways.

The registry also lists a risk ratio of 1.103, with an interval from 0.834 to 1.457, and an odds ratio of 1.226, with an interval from 0.685 to 2.192. Each measure summarizes the same binary endpoint differently. Their intervals include the respective null values for no relative difference, just as the risk-difference interval includes zero. These are unadjusted summary comparisons and do not account for covariates or other design features not described in the registry record.

What does a confidence interval add?

A confidence interval expresses uncertainty around an estimate under the method used to construct it. In general, a wider interval indicates less precision, while an interval spanning the null value does not rule out no difference using that interval’s method. It is not a probability statement that the true effect lies within the particular reported bounds. The primary interval, -0.094 to 0.195, allows effects in both directions and is not narrow enough to support a precise estimate of the contrast.

Why do the reported tests differ across outcomes?

For the primary endpoint, the available comparison is an unadjusted recalculation from posted group counts; a sponsor-reported primary test is not reported in the registry record. The registry reports chi-squared analyses for intracranial bleeding and recurrent ischemic lesion. A chi-squared test assesses whether the observed event distribution differs between groups under its statistical assumptions. The posted p-values are 0.676 and 0.375, respectively. These values do not measure the magnitude or clinical importance of a difference.

Length of hospitalization is reported as a mean and standard deviation: 4.6 with standard deviation 3.9 for rivaroxaban and 5.6 with standard deviation 4.3 for warfarin. The recalculated unadjusted mean difference is 1.0, with an interval from -0.195 to 2.195 and an unadjusted p-value of 0.101. The registry’s own reported analysis is Wilcoxon (Mann-Whitney), with p <.0001. A mean comparison focuses on the difference between arithmetic averages. The Wilcoxon method instead compares the ordering or ranks of observations and is not generally a test of the difference in means. If a distribution is skewed or has outlying values, a rank-based test may respond differently from a mean-based comparison. The individual observation distributions are not reported in the registry record, so the reason for the difference between these analyses cannot be determined from the posted summaries.

When a sponsor-reported analysis is available, it takes precedence over a simple unadjusted recalculation for describing the sponsor’s own analysis. For hospitalization, both are relevant but answer related, not identical, statistical questions. The discrepancy flag is false, but that does not make the two statistical estimands identical.

Why is the event outcome a count of participants?

For the binary endpoints, the outcome is the number of participants with an event. General statistical interpretation distinguishes a participant-level event count from a count of all occurrences: a participant with more than one event may still contribute as a participant with an event, depending on the endpoint definition. The registry labels these outcomes as numbers of participants, and the posted summaries do not give recurrent event totals.

For continuous outcomes, a mean and standard deviation describe the center and spread of observations, respectively. A standard deviation describes variation among observations, rather than uncertainty in the mean. The uncertainty in a group comparison is represented separately by its confidence interval. This distinction is important because the hospitalization means alone do not capture the shape of the data, and the posted standard deviations do not show whether the distributions are symmetric.

All these methods have assumptions and target different quantities. A p-value is not the probability that the null hypothesis is true, and it is not a measure of effect size. Interpretation should combine the estimate, uncertainty interval, endpoint definition, group sizes used for that endpoint, and whether the analysis was reported by the registry or recalculated from summary data. Details such as covariate adjustment, missing-data handling, and prespecified testing choices are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.051, with a confidence interval from -0.094 to 0.195. Because zero lies within this interval, the data do not rule out no difference under the interval’s method. The interval also extends to values in either direction, so the direction and size of the underlying contrast remain uncertain. The estimate should not be read as a precise measure of the treatment effect.

Precision depends on the amount and variability of information available, as well as the method and outcome definition. The primary endpoint combines two types of event, and the posted result is based on the modified intention-to-treat population described in the registry. Differences in endpoint ascertainment, missing observations, or analysis population could affect interpretation, but the details needed to assess these possibilities are not reported in the registry record.

The relative measures also have broad intervals: the risk ratio is 1.103 with an interval from 0.834 to 1.457, and the odds ratio is 1.226 with an interval from 0.685 to 2.192. These intervals include their no-difference values and allow materially different relative contrasts. Different scales can be useful for different questions, but none removes the uncertainty in the underlying evidence.

Confidence intervals are not guarantees about the true effect and do not indicate the probability that a particular treatment is better. Their role is to show the range of values reasonably compatible with the data under the stated method. Here, the breadth of the primary interval is central: the estimate is not sufficiently precise to distinguish a modest benefit, no difference, or a possible disadvantage. A finding that is not statistically significant should not be translated into proof of equivalence.

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 illustrations based on the observed effect, not the trial’s original design calculation. For the binary outcomes, the figures are participants per arm. They are not total participants across both arms. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each scenario targets the stated fraction of the observed effect. The registry record does not report the trial’s own original sample-size assumptions or justification.

The 80% power column describes an illustrative design that would have an 80% chance of detecting the stated effect under those assumptions, if that effect and the assumptions were correct. The 90% power column describes a higher target chance of detection under the same planning framework. These are design targets for a hypothetical future study, not properties observed after this trial was completed.

For example, planning for 75% of the observed effect uses a smaller target effect than planning for the full observed effect, and the listed participant requirement is correspondingly larger. Planning for 50% of the observed effect requires still more participants. In general, smaller effects are harder to distinguish from random variation and therefore require more participants for the same power target.

These figures should be read cautiously because the observed effect from a relatively limited study can be unstable. The illustrations do not account for unreported design details, potential loss to follow-up, or an adjustment for testing multiple outcomes. They are not observed power; post-study calculations of that kind do not replace interpretation of the estimates and confidence intervals. For hospitalization, the planning figures likewise refer to participants per arm, while the special total-event convention applies to time-to-event outcomes; no time-to-event outcome is described among the posted results.

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 = 0.495; treatment proportion p₁ = 0.545; average p̄ = 0.520.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7065 = 1.3848.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7056 = 0.5939.
4. n = (1.3848 + 0.5939)² / (0.0507)² = 1,522.0, rounded up to 1,523 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 <- 0.494736842105263                          # control proportion
p1 <- 0.545454545454545                          # 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(2042534)
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 = 1,523 (80% power), 2,038 (90% power)
 75% of observed effect: n per arm = 2,710 (80% power), 3,627 (90% power)
 50% of observed effect: n per arm = 6,101 (80% power), 8,166 (90% power)
power.prop.test: 1522 
Simulated power at n = 1,523 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. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary composite and several secondary outcomes. When multiple outcomes or analyses are examined, the probability of obtaining at least one small p-value by chance can be greater than for a single prespecified test. Statistical approaches such as adjusted testing procedures or a prespecified hierarchy can address this issue, but the registry record does not report whether such procedures were planned or used. The unadjusted secondary results should therefore be treated as exploratory unless further documentation establishes otherwise.

The registry record also does not report the full statistical analysis plan, including prespecified handling of multiple comparisons, covariate adjustment, interim analyses, or the intended primary hypothesis test. It does not report how missing observations were handled, whether imputation was used, or how participants who discontinued or deviated from treatment were treated in each analysis. Absence of this information is not evidence that a particular procedure was or was not used.

Several analysis populations are named for the primary outcome: modified intention-to-treat, per protocol, and safety. Their group denominators are reported as 95 / 88, 93 / 87, and 98 / 90 for rivaroxaban / warfarin, respectively. The main primary endpoint counts use 95 and 88. These population labels can correspond to different inclusion rules, but the exact rules and reasons for differing denominators are not reported in the registry record. Results from different populations can answer different questions and may be affected differently by exclusions or missing data.

Randomization helps support a fair comparison at assignment, while analysis choices after randomization can affect how well that comparison is preserved. Without more detail on population definitions, missingness, and the analysis plan, it is not possible to assess the sensitivity of the findings to those choices. These reporting gaps do not invalidate the posted results, but they limit independent evaluation of their robustness.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: vertigo positional (1.1%), laboratory test abnormal (1.1%), arthritis (1.1%), cerebral infarction (1.1%), pulmonary hypertension (1.1%).

The safety summaries report serious adverse events affecting 6 of 98 participants in the rivaroxaban group and 5 of 90 in the warfarin group. Other adverse events affected 46 of 98 and 51 of 90, respectively. These are participant counts and denominators for the safety groups; they are not the same populations as the primary endpoint analysis groups. The registry does not report deaths in the safety summary.

The listed serious adverse event terms with the highest reported percentages include positional vertigo, laboratory test abnormal, arthritis, cerebral infarction, and pulmonary hypertension, each listed as 1.1%, and atrial fibrillation, listed as 1.0%. The record does not provide enough detail in these summaries to infer severity beyond the serious-event classification, timing, causality, or whether an event occurred in one group or both. The figures should be read as descriptive safety reporting, not as a complete comparative safety analysis.

Differences in adverse-event counts do not, by themselves, show that a treatment caused or prevented an event. Interpretation depends on definitions, follow-up, exposure, event ascertainment, and the relevant analysis population. Those details are not fully reported in the registry record.

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

The posted results describe a randomized comparison of early rivaroxaban and warfarin strategies in acute ischemic stroke associated with atrial fibrillation. For the primary imaging composite at 1 month after randomization, the estimated risk difference is 0.051, with a confidence interval from -0.094 to 0.195 and an unadjusted p-value of 0.493. The estimate is uncertain and does not demonstrate a clear difference between the groups.

This does not establish that the strategies are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the effect falls within that margin; such information is not reported in the registry record. Nor does the result prove that no difference exists. The confidence interval spans zero and allows a range of possible effects, which is a statement about imprecision rather than proof of sameness.

The primary outcome is a composite of bleeding and recurrent ischemic lesions, so its result does not by itself identify the separate balance of those components. Secondary outcomes provide additional descriptive information, but the registry’s unadjusted analyses and missing details about multiplicity limit the strength of confirmatory claims. The hospitalization result also illustrates why test methods matter: the reported Wilcoxon analysis and the recalculated mean comparison address different features of the data.

The record cannot answer every practical question about treatment implementation, longer-term outcomes, adherence, or the generalizability of the findings. The study is phase 2, and the registry record does not report a sample-size justification or complete analysis plan. Safety summaries are descriptive and do not establish causation. The appropriate interpretation is therefore limited to the posted estimates, their uncertainty, the specified endpoints, and the study population and follow-up described in the registry.

17. Why This Trial Matters Statistically

This trial is statistically interesting because its main question involves two different types of harm: intracranial bleeding and recurrent ischemic lesions. Combining them into a primary endpoint can summarize an overall event experience, but the combined result needs to be understood alongside the component outcomes. Otherwise, a single estimate may conceal distinct patterns across outcomes with different clinical meanings.

The posted primary estimate also illustrates the difference between an effect estimate and a test of statistical significance. The risk difference provides a direction and scale for the contrast, while its confidence interval communicates substantial uncertainty. The unadjusted p-value alone cannot show whether a possible difference is important or how precisely it has been estimated. Reading the estimate, interval, endpoint definition, and group counts together gives a fuller interpretation.

The hospitalization outcome offers a second statistical lesson: a mean-based comparison and a rank-based test can produce different results because they do not target exactly the same feature of the data. The registry reports both a Wilcoxon analysis and summary statistics that permit an unadjusted mean comparison. Recognizing the distinction prevents a p-value from being treated as a universal description of the outcome.

Finally, the planning illustrations show how sample-size requirements depend on the effect a future study aims to detect. Smaller target effects require more participants under the stated assumptions. These illustrations are not evidence that the completed trial was adequately powered for its original objectives; the original design assumptions are not reported in the registry record. Together, these features make the trial a useful example of why statistical interpretation depends on design, endpoint construction, analysis choices, and precision—not on a single threshold.

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 result is imprecise, and the registry record does not report a sample-size justification that would clarify the precision the investigators intended to achieve. The study is phase 2, and its enrollment and posted endpoint populations should be considered when interpreting the breadth of the estimates. The planning illustrations based on observed effects are not a substitute for the original design calculation.

The trial used no masking. The registry record does not report details of allocation concealment, endpoint adjudication, assessor masking, adherence, or treatment discontinuation. Since the primary outcome includes imaging findings, information about consistent image assessment would help readers judge the potential for assessment differences; such details are not reported in the registry record.

The primary endpoint combines intracranial bleeding and recurrent ischemic lesion, which may differ in clinical importance and occurrence. Separate secondary outcomes are listed, but the registry record does not report the result for modified Rankin Score of 0 or 1 at Week 4. The short primary timeframe is 1 month after randomization, so the posted primary result does not describe longer-term outcomes.

Analysis details are incomplete. The statistical analysis plan, multiplicity strategy, missing-data procedures, exact definitions of analysis populations, and any interim analyses are not reported in the registry record. The hospitalization result also has a reported rank-based test alongside an unadjusted mean-based recalculation; the observation-level data needed to understand their differing results are unavailable in the registry summaries. These limitations constrain interpretation and generalization without changing what the posted counts and estimates state.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Rivaroxaban Versus Warfarin in Acute Ischemic Stroke With Atrial Fibrillation — NCT02042534.
• Registry record last updated 2017-02-08; status last verified 2016-12.
• Results first posted 2017-02-08.
• 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 describes a completed, randomized, parallel-group, phase 2 trial with no masking, comparing rivaroxaban with warfarin in acute ischemic stroke associated with atrial fibrillation. Enrollment is listed as 195, and the primary endpoint is the number of participants with intracranial bleeding and/or recurrent ischemic lesion confirmed by imaging 1 month after randomization.

The primary comparison reports a risk difference of 0.051, with a confidence interval from -0.094 to 0.195 and an unadjusted p-value of 0.493. The interval spans zero and indicates substantial uncertainty about the direction and size of the difference. Secondary outcomes and safety counts provide additional context, but unreported analysis details and multiplicity procedures limit firm interpretation.

The registry record does not report the original sample-size justification, full statistical analysis plan, missing-data procedures, or a result for every listed secondary outcome. The posted results should be interpreted as estimates for the recorded study population and follow-up, not as proof of equivalence or a definitive overall treatment advantage.