Comparison of Bleeding Risk Between Rivaroxaban and Apixaban for the Treatment of Acute Venous Thromboembolism: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Bleeding Risk Between Rivaroxaban and Apixaban for the Treatment of Acute Venous Thromboembolism (NCT03266783), a randomized phase 4 study. The primary outcome is The Rate of Adjudicated Clinically Relevant Bleeding (CRB) Events.

2. Clinical Question

3. Trial Design

This was a phase 4 randomized, parallel-group trial with no masking listed in the design fields. The brief summary describes it as a multi-center, pragmatic, prospective, randomized, open-label trial with blinded endpoint assessment. That description is commonly abbreviated as PROBE: treatment assignment is open, while endpoint assessment is blinded. The record lists Ottawa Hospital Research Institute as sponsor and an enrollment of 2760.

The two treatment groups received different oral dosing schedules. The apixaban schedule was 10 mg twice a day for 1 week, then 5 mg twice a day for 3 months of treatment. The rivaroxaban schedule was 15 mg twice a day for 3 weeks, then 20 mg once a day for 3 months of treatment. The primary outcome was assessed for the duration of the study: 3 months. The record status is completed; the listed start date is 2017-12-13 and primary completion date is 2025-04-30.

Random allocation is intended to make assigned groups comparable on average, including for factors that may affect outcomes. It does not ensure that groups are identical, and it does not remove the need to consider how outcomes were assessed, how missing information was handled, or which participants were included in analyses. The record does not report the allocation procedure or concealment details. It also does not report the trial’s original sample-size justification, its planned analysis population, or the analysis methods in enough detail to establish how those issues were handled.

The primary outcome is described as a count of participants with an event, rather than a rate expressed per unit of follow-up. The registry lists 1345 participants in the apixaban group and 1355 in the rivaroxaban group for this outcome. Those are the group denominators shown with the posted result; they should not be confused with the registry’s enrollment field.

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

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 The Rate of Adjudicated Clinically Relevant Bleeding (CRB) Events, measured over For the duration of the study: 3 months.

The primary endpoint is the number of participants with an adjudicated clinically relevant bleeding event during the 3-month study period. The registry defines this composite outcome as major bleeding events together with clinically relevant non-major bleeding events. The posted counts are 44 in the apixaban group and 96 in the rivaroxaban group.

A composite endpoint combines more than one type of event under a single outcome definition. This can capture a broader range of clinically relevant events than major bleeding alone, while making interpretation dependent on the components included. In this trial, major bleeding and clinically relevant non-major bleeding are both included, and each is also listed as a secondary outcome. The primary result therefore concerns the combined endpoint; it should not be read as if every event was a major bleed.

Adjudication indicates that events were assessed against the outcome definition rather than simply counted without review. The brief summary describes blinded endpoint assessment, which can help limit the influence of knowledge of assigned treatment on endpoint assessment. The record does not give further detail on adjudication procedures or on how disagreements were resolved.

Bleeding was selected as the primary safety question because the trial’s stated aim was to compare the safety of apixaban and rivaroxaban for VTE treatment. The endpoint addresses that question over the stated treatment period. It does not, by itself, summarize recurrent VTE, mortality, adherence, quality of life, or cost-effectiveness; those topics appear among the secondary outcomes.

7. Results Posted in the Registry

• Rivaroxaban Group: 7.1% (96/1355) versus 3.3% (44/1345) on control; risk difference 3.8 percentage points (95% CI 2.1 to 5.5), risk ratio 2.17 (1.53–3.07); unadjusted two-proportion z-test p = <0.001.

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 Adjudicated Major Bleeding Events

• 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:
  • Rivaroxaban Group: 2.4% (32/1355) versus 0.4% (5/1345) on control; risk difference 2.0 percentage points (95% CI 1.1 to 2.9), risk ratio 6.35 (2.48–16.25); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Rivaroxaban Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Adjudicated Clinically Relevant Non-Major Bleeding Events

• 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:
  • Rivaroxaban Group: 4.9% (67/1355) versus 2.9% (39/1345) on control; risk difference 2.0 percentage points (95% CI 0.6 to 3.5), risk ratio 1.71 (1.16–2.51); unadjusted two-proportion z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Rivaroxaban Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Adjudicated Recurrent Venous Thromboembolism (VTE) Events

• 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:
  • Rivaroxaban Group: 1.0% (14/1355) versus 1.1% (15/1345) on control; risk difference -0.1 percentage points (95% CI -0.9 to 0.7), risk ratio 0.93 (0.45–1.91); unadjusted two-proportion z-test p = 0.836.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rivaroxaban Group 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 by separating its major-bleeding and clinically relevant non-major-bleeding components and by including recurrent VTE, VTE-related death, all-cause mortality, medication adherence, quality-adjusted life years, and cost-effectiveness. Across the posted component counts, the direction is consistent with the primary result: both bleeding components have higher counts in the rivaroxaban group. The recurrent VTE counts are similar between the groups, and this comparison does not show a clear group separation in the posted unadjusted test.

These secondary outcomes help identify which aspects of the clinical question were considered, but they do not replace the primary endpoint. Component outcomes can clarify what contributes to a composite, while outcomes such as recurrent VTE and mortality address different aspects of treatment. The interpretation of each depends on its event frequency, precision, and analysis, not merely on whether its direction matches the primary finding.

Unadjusted secondary results carry less weight than the primary comparison because multiple outcomes can generate opportunities for apparently notable findings. The registry lists secondary outcomes, but does not report a multiplicity adjustment or a full statistical analysis plan. Without such information, p-values for secondary comparisons should be treated as exploratory rather than as a set of confirmatory tests. Lack of a statistically clear difference also does not establish equivalence or rule out a meaningful difference; precision and the range of estimates matter.

The record lists nine secondary outcomes as posted, while the outcome details available for comparison include the three bleeding, recurrent VTE, and death-related outcomes plus other listed measures. Results for adherence, quality-adjusted life years, and cost-effectiveness are not reported in the registry record summarized for these comparisons. The secondary evidence therefore adds context but does not provide a complete accounting of every listed outcome.

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

• Number of Participants With Adjudicated Major Bleeding Events
• Number of Participants With Adjudicated Clinically Relevant Non-Major Bleeding Events
• Number of Participants With Adjudicated Recurrent Venous Thromboembolism (VTE) Events
• Number of Participants With Adjudicated VTE-Related Deaths
• All-cause Mortality
• Medication Adherence
• Quality-Adjusted Life Years (QALYs) Gained
• Incremental Cost-effectiveness Ratio

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: each participant is classified according to whether an adjudicated clinically relevant bleeding event was recorded during the stated period. The posted group counts are compared with their group denominators, and the registry presents group risks and measures of between-group association. These summaries are unadjusted; the record does not list a covariate-adjusted primary estimate.

What does a risk difference express?

In general, a risk difference subtracts the event risk in one group from the event risk in the other. Its scale is the absolute difference in risk, which can be useful for communicating how far apart the observed group risks are. The registry’s estimate is oriented as rivaroxaban minus apixaban. The posted risk difference is 0.038, with a 95% confidence interval from 0.021 to 0.055. A positive value on this orientation means the observed risk is higher in the rivaroxaban group. The interval describes uncertainty about the estimated difference under the method used; it does not describe the range of individual outcomes.

How do relative measures differ?

In general, a risk ratio divides one group’s risk by the other group’s risk, whereas an odds ratio compares the groups’ odds of an event. These measures use relative rather than absolute scales. The registry reports a risk ratio of 2.166 (95% confidence interval 1.528 to 3.069) and an odds ratio of 2.255 (95% confidence interval 1.565 to 3.248). Risk ratios and odds ratios can differ, particularly as event risks become less rare. They answer related but distinct descriptive questions; neither should be substituted silently for the risk difference.

What does the p-value contribute?

In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, nor does it quantify the size or practical importance of the result. The primary unadjusted p-value is < 0.001. That value is consistent with the confidence interval excluding zero for the risk difference, but the confidence interval is also important because it presents a range of estimates compatible with the data and method.

The registry labels the comparison unadjusted. No adjustment for baseline covariates is reported in the comparison, and the record does not describe a model used to account for other factors. Randomization is the design feature that supports a comparison of assigned groups, but unadjusted analysis does not mean every possible source of error has been addressed. The record does not report allocation concealment, adherence to assigned treatment, crossover, or the primary analysis population.

The registry reports participant counts and risks rather than a time-to-event estimate. Therefore, the posted primary comparison does not describe when bleeding occurred within the study period or account for differences in time to event. The record states the primary outcome timeframe as 3 months, but does not report a time-to-event analysis for the primary result.

Adjudicated endpoint assessment is relevant because the outcome requires applying definitions of major and clinically relevant non-major bleeding. The brief summary describes blinded endpoint assessment despite open-label treatment assignment. In general, blinding an endpoint assessment can reduce the chance that knowledge of group assignment influences outcome classification. The record does not report the adjudication charter or further procedural details, so the degree and implementation of blinding cannot be evaluated from the registry record.

The risk difference, risk ratio, odds ratio, confidence intervals, and p-value are multiple descriptions of the primary comparison, not separate outcome measurements. They use the posted group data and characterize different aspects of the same contrast. The registry identifies no reported analyses in the analysis fields for the primary comparison, so detailed choices such as the confidence-interval method, continuity corrections, or handling of missing observations are not reported in the registry record.

11. Confidence Intervals and Precision

The primary risk difference is 0.038, with a 95% confidence interval from 0.021 to 0.055. The lower and upper limits are both above zero. This gives the estimate a direction consistent with a higher posted risk in the rivaroxaban group, while the width of the interval indicates that the exact size of the difference remains uncertain. The interval is not a range guaranteed to contain the true effect, nor does it indicate where individual participant outcomes will fall.

In general, a confidence interval expresses the precision of an estimate under the statistical method used. A narrower interval indicates less sampling uncertainty on that scale, while a wider interval indicates more. The interval for the primary risk difference allows a range of positive estimates, rather than identifying a single exact difference. It does not account automatically for possible bias, differences in how outcomes were recorded, missing data, or limits in the trial’s applicability.

The relative estimates also have intervals: the risk ratio is 2.166, with a 95% confidence interval from 1.528 to 3.069, and the odds ratio is 2.255, with a 95% confidence interval from 1.565 to 3.248. Those ranges are on different scales from the risk-difference interval. Their numerical widths cannot be compared directly to decide which measure is more precise.

The event counts are modest relative to the group denominators, so individual events can affect the estimated risks. The record does not report confidence intervals for the group risks themselves, or details of the methods used to calculate the posted intervals. Precision should therefore be read from the reported estimates and intervals without assuming additional adjustments or robustness analyses.

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 illustrations are expressed as participants per arm for 80% power and participants per arm for 90% power. They are not totals across both arms. They are based on the stated fraction of the observed effect for the relevant outcome; the listed illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The record does not report the trial’s own original sample-size assumptions or justification.

The 80% power column gives the modeled participants per arm for a future study to have an 80% chance of detecting the specified effect under those planning assumptions, if that effect and the assumptions are correct. The 90% column gives the corresponding per-arm planning figure for 90% power. Power is a design property for a specified effect and analysis plan; it is not a measure of the probability that the observed result is true.

The rows describing planning for 100%, 75%, and 50% of the observed effect show how the required sample size changes when the target difference is made smaller. Smaller effects are harder to distinguish from random variation, so they require more participants under otherwise unchanged assumptions. The required numbers can become very large for outcomes with a small observed difference, as illustrated by the recurrent VTE comparison.

These are planning illustrations based on the observed effect, not observed power. They do not show the power of the completed trial, and they should not be treated as the trial’s original design calculation. The planning figures also rely on assumptions that may not match a future study’s population, event risk, follow-up, or analysis choices. For time-to-event outcomes, the stated convention is total events; the other planning illustrations are participants per arm. The posted outcomes discussed in these illustrations are participant event counts, so the per-arm convention applies.

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 = 0.033; treatment proportion p₁ = 0.071; average p̄ = 0.052.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3134 = 0.6142.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3122 = 0.2628.
4. n = (0.6142 + 0.2628)² / (0.0381)² = 528.8, rounded up to 529 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 <- 0.0327137546468401                          # control proportion
p1 <- 0.0708487084870849                          # 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(3266783)
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 = 529 (80% power), 708 (90% power)
 75% of observed effect: n per arm = 859 (80% power), 1,149 (90% power)
 50% of observed effect: n per arm = 1,746 (80% power), 2,337 (90% power)
power.prop.test: 528.8 
Simulated power at n = 529 per arm: 0.810 (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 outcome and multiple secondary outcomes. Testing or estimating many outcomes creates a multiplicity issue: even when no underlying differences exist, examining many comparisons can increase the chance of finding an apparently unusual result. A prespecified hierarchy or statistical adjustment can address this concern, but the registry record does not report a multiplicity plan or adjustment. The posted secondary p-values are therefore unadjusted, and should not be interpreted as if they came from a single isolated confirmatory test.

The primary comparison is the clearest focal analysis because it is identified as the primary outcome. The primary p-value is also unadjusted, and the record does not supply enough detail to determine whether any other planned testing structure applied. The statistical analysis plan, any interim analyses, and rules for handling multiple endpoints are not reported in the registry record.

Missing-data handling is also not reported in the registry record. The record does not state how participants without complete outcome information were treated, whether missingness occurred, or whether sensitivity analyses were conducted. The listed outcome denominators are reported for each group, but those counts alone do not establish the completeness of follow-up or explain how those denominators were selected.

The analysis population is not reported in the registry record. In particular, the available details do not establish whether the primary comparison followed an intention-to-treat approach, included participants according to treatment received, or used another population definition. The record also does not report treatment discontinuations, crossovers, protocol deviations, or per-protocol analyses. These details matter because they can affect what a group comparison estimates.

Randomization, blinded endpoint assessment, and adjudication are relevant strengths of the described design, but they cannot substitute for information about analysis populations, missing outcomes, or multiplicity. Without those details, the primary finding can be described using the posted unadjusted estimate and interval, while the extent to which alternative analytic choices would change the result remains uncertain.

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

Serious events with the highest arm-level rate: chest pain, myocardial infarction, atrial fibrillation, cardiovascular disease, cardiac arrest (0.7%), pneumonia, viral infection, appendicitis, fever, empyema, abscess, sepsis (0.6%), lung cancer, ovarian cancer, pancreatic cancer, lymphoma, adenocarcinoma (0.4%), obstruction, intussusception, hernia, inflammatory bowel syndrome, ischemia, mesenteric thrombosis (0.4%), headache, limb weakness, neuropathy, stroke (0.3%).

The adverse-event record lists serious adverse events affecting 36 participants in the apixaban group and 30 in the rivaroxaban group. It also lists 1 death in the apixaban group and 4 in the rivaroxaban group. These are registry safety figures, not the primary adjudicated bleeding endpoint, and the record does not report a statistical comparison or causal attribution for these counts.

The listed serious-event terms are grouped categories, including cardiovascular terms at 0.7%, infection-related terms at 0.6%, cancer-related terms at 0.4%, obstruction and gastrointestinal or vascular terms at 0.4%, neurologic terms at 0.3%, and suicidal ideation or hallucinations at 0.2%. These categories combine different diagnoses and should not be interpreted as a single uniform event type. The record lists zero in the fields for other adverse events affected and at risk for both groups; that reporting does not establish that no other events occurred outside those fields.

Serious adverse events are broader than bleeding, and the posted counts do not establish that treatment caused an event. Differences in these counts should be read descriptively because no comparative estimate or inferential analysis is reported for them.

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

The result means that, in the randomized groups and during the stated 3-month period, the registry recorded more participants with adjudicated clinically relevant bleeding in the rivaroxaban group than in the apixaban group. The unadjusted risk difference is 0.038, with a 95% confidence interval from 0.021 to 0.055 and p < 0.001. This is the principal statistical finding for the endpoint defined in the record.

It does not mean that every participant assigned to rivaroxaban experienced bleeding, or that participants assigned to apixaban had no bleeding. It also does not mean that the observed difference is an exact prediction for another population or treatment setting. The confidence interval reflects uncertainty from the comparison under its calculation method, while other sources of uncertainty, including missing-data handling and unreported analytic choices, are not resolved by that interval.

The endpoint combines major and clinically relevant non-major bleeding. Therefore, the primary estimate is not an estimate of major bleeding alone. The component counts provide additional context, but secondary comparisons are unadjusted and the registry does not report a multiplicity plan. The primary finding should not be taken to settle every safety question.

The trial also considered recurrent VTE, death, medication adherence, quality-adjusted life years, and cost-effectiveness. The bleeding result alone cannot establish an overall balance across those outcomes. Nor does the result establish a treatment recommendation or determine which option is appropriate for a particular person. The posted data describe group outcomes in this trial, with its stated eligibility, treatment schedules, endpoint definition, and follow-up.

Randomization and blinded endpoint assessment are meaningful features of the described study design, but a registry record is not a full account of trial conduct. Details about missing data, analysis populations, protocol adherence, and multiplicity are not reported in the registry record. Those omissions limit how comprehensively the statistical analysis can be assessed from the posted information.

17. Why This Trial Matters Statistically

This trial addresses a direct comparison between apixaban and rivaroxaban for acute VTE treatment. The registry summary notes that both drugs had been compared with standard therapy in randomized trials, while direct head-to-head safety and efficacy data were described as unavailable. A randomized comparison can contribute evidence that differs from indirect comparisons across separate studies, because both assigned treatments are evaluated within the same trial framework.

The primary outcome is clinically relevant bleeding, a safety endpoint that combines major and clinically relevant non-major events. That definition makes the endpoint broader than major bleeding alone and gives the result a specific interpretation: it concerns participants meeting the combined adjudicated definition during the stated treatment period. Separating the components as secondary outcomes can add context, while the composite remains the primary question.

From a statistical perspective, the trial illustrates why the effect scale matters. The risk difference describes the absolute separation between group risks, whereas the risk ratio and odds ratio describe relative contrasts. Confidence intervals show uncertainty around each estimate, and the p-value does not replace either the effect size or the interval. Considering these together provides a more informative reading than treating a thresholded p-value as the whole result.

The study also highlights limits of registry-based interpretation. The record identifies a randomized, open-label design with blinded endpoint assessment and provides outcome counts, but does not report important details such as the analysis population, missing-data methods, multiplicity strategy, or original sample-size rationale. These gaps do not erase the posted result, but they constrain assessment of how robustly it represents the intended comparison.

Finally, the secondary outcomes remind readers that a safety comparison is not equivalent to an overall treatment comparison. Bleeding, recurrent VTE, death, adherence, quality of life, and cost-effectiveness address distinct questions. A sound statistical interpretation keeps the primary result in focus while recognizing that the wider clinical and economic picture cannot be inferred from this endpoint alone.

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 registry record does not report the original sample-size justification, so the relationship between the trial’s planned enrollment and its anticipated primary effect cannot be assessed from the available information. The planning illustrations based on observed effects are not a substitute for the original rationale.

The record identifies the study as open-label, with blinded endpoint assessment described in the summary. It does not provide details about how endpoint adjudication was implemented, whether adjudicators remained blinded in practice, or how disagreements were resolved. The primary endpoint depends on applying definitions of major and clinically relevant non-major bleeding, making these procedures relevant to interpretation.

Key analytic details are not reported in the registry record: the primary analysis population, missing-data methods, handling of treatment discontinuation or crossover, covariate adjustment, and multiplicity strategy. No reported analysis details establish whether all randomized participants were analyzed as assigned. The posted comparison is unadjusted.

The primary outcome is limited to the 3-month period and combines bleeding events rather than describing timing or severity distributions in detail. The registry lists additional outcomes, but results for several listed measures are not reported in the registry record. The safety figures also lack a comparative analysis and causal attribution.

Finally, the group results pertain to the trial’s enrolled population and specific dosing schedules. The registry record does not provide enough eligibility or site-level detail in the summarized information to assess how well these results apply to every VTE population or treatment setting. These limitations call for a focused reading of the endpoint and its reported uncertainty rather than broad conclusions about all outcomes or contexts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison of Bleeding Risk Between Rivaroxaban and Apixaban for the Treatment of Acute Venous Thromboembolism — NCT03266783.
• Registry record last updated 2026-06-24; status last verified 2026-05.
• Results first posted 2026-06-24.
• 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 NCT03266783 as a completed phase 4, randomized, parallel-group comparison of apixaban and rivaroxaban for acute VTE. It lists no masking in the design fields; the brief summary describes an open-label trial with blinded endpoint assessment. Ottawa Hospital Research Institute is listed as sponsor, and the registry enrollment is 2760.

The primary endpoint was the number of participants with adjudicated clinically relevant bleeding during 3 months, defined as major plus clinically relevant non-major bleeding. The posted counts were 44 in the apixaban group and 96 in the rivaroxaban group. The unadjusted risk difference was 0.038 (95% confidence interval 0.021 to 0.055; p < 0.001).

The record also lists secondary bleeding, recurrent VTE, mortality, adherence, quality-of-life, and cost-effectiveness outcomes. The analysis population, missing-data handling, multiplicity plan, and original sample-size rationale are not reported in the registry record.