Efficacy and Safety of Rivaroxaban in Reducing the Risk of Major Thrombotic Vascular Events in Subjects With Symptomatic Peripheral Artery Disease Undergoing Peripheral Revascularization Procedures of the Lower Extremities: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Rivaroxaban in Reducing the Risk of Major Thrombotic Vascular Events in Subjects With Symptomatic Peripheral Artery Disease Undergoing Peripheral Revascularization Procedures of the Lower Extremities (NCT02504216), a randomized phase 3 study. The primary outcome is Primary Efficacy Outcome: Number of Participants With Composite of Myocardial Infarction (MI), Ischemic Stroke, Cardiovascular Death, Acute Limb Ischemia (ALI) and Major Amputation Due to a Vascular Etiology.

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, phase 3 trial with quadruple masking and a placebo control. The registry lists Bayer as the sponsor and the study status as completed. Enrollment was 6564. The recorded start date was 2015-08-18, and the primary completion date was 2019-11-27. These registry dates do not, by themselves, describe each participant’s length of follow-up.

The two assigned regimens were rivaroxaban 2.5 mg twice daily plus aspirin 100 mg once daily, and rivaroxaban-placebo twice daily plus aspirin 100 mg once daily. Randomization supports a comparison of assigned groups, while masking is intended to limit the influence of treatment knowledge on participants’ experiences and outcome assessment. The registry does not specify which parties were included in the quadruple masking.

The primary efficacy analysis used the intention-to-treat set, defined in the record as all randomized participants. The outcome was the first occurrence of the composite after randomization through the efficacy cut-off date of 08-Sep-2019. The registry reports a mean time in follow-up survival time until that date of 1109.76 days. The original sample-size justification, allocation ratio details beyond the randomized groups, follow-up procedures, and planned interim analyses are not reported in the registry record.

The treatment contrast is specifically the addition of rivaroxaban to aspirin in this post-revascularization population. It is not a comparison with no antithrombotic treatment, and it does not isolate the effect of aspirin. The record’s brief summary describes the clinical rationale in terms of vascular events affecting the heart, brain, and legs. The numerical results should be interpreted for the stated outcomes and trial population rather than generalized to other populations or treatment settings.

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: A total of 6772 participants were screened, of which 6564 were randomly assigned to either of the two treatment arms.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention-to-treat analysis set (ITT Set): Comprised all randomized participants.

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 Primary Efficacy Outcome: Number of Participants With Composite of Myocardial Infarction (MI), Ischemic Stroke, Cardiovascular Death, Acute Limb Ischemia (ALI) and Major Amputation Due to a Vascular Etiology, measured over For each participant, the first occurrence of the composite primary efficacy outcome after randomization up until the efficacy cut-off date (08-Sep-2019) was considered. The mean time in follow-up survival time until ECOD that date was 1109.76 days..

The primary endpoint is a composite of myocardial infarction, ischemic stroke, cardiovascular death, acute limb ischemia, and major amputation due to a vascular etiology. For each participant, the registry counted the first occurrence of any component after randomization through the efficacy cut-off date, 08-Sep-2019. A participant with more than one component contributes the first qualifying event to this endpoint, rather than a count of every event.

Composite endpoints are used to capture a broader set of clinically important events and can increase the number of observed events available for comparison. That can make a trial’s overall outcome more informative than considering a rare component alone. But the components may differ in severity, frequency, and clinical meaning. A composite result therefore does not establish that every component moved in the same direction or contributed equally. Component-specific results are not reported in the primary outcome details.

The registry reports 508 participants with the primary outcome in the rivaroxaban-plus-aspirin group and 584 in the placebo-plus-aspirin group. These are participant counts over the stated outcome window. They do not, on their own, account for when events occurred or differences in time under observation. The sponsor’s reported log-rank analysis addresses time to the event, whereas the simple recalculation compares the posted participant counts as proportions. Those approaches answer related but distinct statistical questions.

7. Results Posted in the Registry

• Rivaroxaban 2.5 mg Bid + Aspirin 100 mg od: 15.5% (508/3286) versus 17.8% (584/3278) on control; risk difference -2.4 percentage points (95% CI -4.2 to -0.6), risk ratio 0.87 (0.78–0.97); unadjusted two-proportion z-test p = 0.010.

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 Composite of MI, Ischemic Stroke, Coronary Heart Disease (CHD) Death, ALI, and Major Amputation of a Vascular Etiology

• 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 2.5 mg Bid + Aspirin 100 mg od: 13.2% (433/3286) versus 16.1% (528/3278) on control; risk difference -2.9 percentage points (95% CI -4.6 to -1.2), risk ratio 0.82 (0.73–0.92); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Rivaroxaban 2.5 mg Bid + Aspirin 100 mg od than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With an Unplanned Index Limb Revascularization for Recurrent Limb Ischemia (Subsequent Index Leg Revascularization That Was Not Planned or Considered as Part of the Initial Treatment Plan at the Time of Randomization)

• 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 2.5 mg Bid + Aspirin 100 mg od: 17.8% (584/3286) versus 20.0% (655/3278) on control; risk difference -2.2 percentage points (95% CI -4.1 to -0.3), risk ratio 0.89 (0.80–0.98); unadjusted two-proportion z-test p = 0.022.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Rivaroxaban 2.5 mg Bid + Aspirin 100 mg od than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With Hospitalization for a Coronary or Peripheral Cause (Either Lower Limb) of a Thrombotic Nature

• 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 2.5 mg Bid + Aspirin 100 mg od: 8.0% (262/3286) versus 10.9% (356/3278) on control; risk difference -2.9 percentage points (95% CI -4.3 to -1.5), risk ratio 0.73 (0.63–0.85); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Rivaroxaban 2.5 mg Bid + Aspirin 100 mg od than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The detailed secondary results available in the registry point in the same general direction as the primary result: the posted participant counts for the described secondary composites and limb revascularization outcome are lower in the rivaroxaban-plus-aspirin group than in the placebo-plus-aspirin group. The corresponding reported hazard ratios are also below 1. This directional consistency can make the primary pattern less isolated, but secondary outcomes remain supportive context rather than a substitute for the primary analysis.

These secondary endpoints cover different event definitions, including composites involving vascular events, recurrent limb revascularization, and hospitalization for a thrombotic coronary or peripheral cause. Their clinical meaning and component composition differ. Results from one endpoint should not be assumed to establish effects on another endpoint, and the reported secondary comparisons do not establish that each component within a composite follows the overall pattern.

Unadjusted secondary p-values carry less weight when multiple outcomes are tested. As a general statistical principle, considering many tests without an adjustment increases the chance that some results appear statistically notable by chance, even when there is no corresponding effect. The registry does not report a multiplicity adjustment or a prespecified hierarchy for interpreting the secondary outcomes. Therefore, the secondary findings are best treated as exploratory or supportive unless additional analysis-plan information is available.

The record lists other secondary outcomes, but detailed numerical results for those outcomes are not reported in the registry record. That limits assessment of whether the overall pattern extends across every listed endpoint. The available results should be interpreted alongside the primary endpoint, with attention to their differing definitions and the lack of reported multiplicity procedures.

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

• Number of Participants With Composite of MI, Ischemic Stroke, Coronary Heart Disease (CHD) Death, ALI, and Major Amputation of a Vascular Etiology
• Number of Participants With an Unplanned Index Limb Revascularization for Recurrent Limb Ischemia (Subsequent Index Leg Revascularization That Was Not Planned or Considered as Part of the Initial Treatment Plan at the Time of Randomization)
• Number of Participants With Hospitalization for a Coronary or Peripheral Cause (Either Lower Limb) of a Thrombotic Nature
• Number of Participants With Composite of MI, Ischemic Stroke, All-cause Mortality (ACM), ALI, and Major Amputation of a Vascular Etiology
• Number of Participants With Composite of MI, All-cause Stroke, Cardiovascular (CV) Death, Acute Limb Ischemia (ALI), and Major Amputation of a Vascular Etiology
• Number of Mortality (All-cause)
• Number of Participants With Venous Thromboembolic (VTE) Events
• Secondary Safety Outcome: Number of Participants With ISTH (International Society on Thrombosis and Haemostasis) Major Bleeding

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level for the posted count comparison: each participant is classified according to whether a first qualifying composite event occurred during the stated period. The raw event counts are 508 among 3286 participants assigned rivaroxaban plus aspirin and 584 among 3278 assigned placebo plus aspirin. The registry also presents a time-to-event analysis, which uses information about when the event occurred and can account for different observed follow-up times in ways that a simple proportion comparison does not.

What does the risk difference represent?

The risk difference is the intervention-group risk minus the comparator-group risk. For the primary outcome, the recalculated estimate is -0.024, with a 95% confidence interval from -0.042 to -0.006. A negative value means the observed proportion with the event was lower in the rivaroxaban group. The interval describes a range of values compatible with the data under the calculation’s statistical assumptions. It is not a guarantee that the true difference lies within that range, and it does not account for unreported features of the trial analysis.

The recalculation uses the posted counts and group sizes and is unadjusted. It is not the same analysis as the sponsor’s log-rank result. The record gives p = 0.01 for the unadjusted recalculation; the sponsor reports p = 0.004 for the log-rank analysis. Differences between these values can arise because the methods use the data differently. They should not be read as competing versions of one identical calculation.

What does the log-rank result add?

The log-rank method compares event-time experience between groups over follow-up. The registry reports a hazard ratio of 0.85 and a 95% confidence interval from 0.76 to 0.96. In general, a hazard ratio compares the instantaneous event rates between groups at a given point in follow-up among participants who have not yet had the event. Its interpretation depends on the structure of the time-to-event data and the model assumptions. Details of those assumptions and diagnostics are not reported in the registry record. The log-rank p-value tests whether the observed event-time patterns are compatible with a null comparison under that method; it does not measure the probability that the null hypothesis is true.

The registry identifies the analysis as a superiority analysis. That label describes the testing objective, not a guarantee about clinical importance or the quality of every component of the endpoint. The reported hazard ratio and its interval are the sponsor’s analysis, while the crude risk difference and its interval are recalculated from the posted summary counts. The record does not flag a discrepancy between these summaries.

Why can over-dispersion matter?

Over-dispersion is a general statistical concern when outcome variability is greater than a model expects. It can make standard errors too small and confidence intervals too narrow if a method assumes less variability than is present. The primary endpoint is recorded as participants with a binary event, and no over-dispersion parameter is reported. Over-dispersion is more directly relevant to certain count models; it should not be invoked as a diagnosis of this analysis without evidence in the record. More broadly, the suitability of any statistical model depends on its assumptions and the observed data structure.

Randomization and intention-to-treat analysis address different design and analysis concerns. Randomization aims to make assigned groups comparable at baseline, on average. Intention-to-treat retains participants in their assigned groups for analysis, regardless of later treatment received, according to the registry’s definition of the analysis set. The record states that the primary population included all randomized participants, but does not provide detailed rules for missing outcome information or departures from assigned treatment.

The primary efficacy window ended at the stated efficacy cut-off date, and the registry reports a mean survival time until that date of 1109.76 days. The mean is a summary of follow-up, not a description of every participant’s observation time. Details such as censoring rules, the shape of the event-time distributions, and proportional-hazards assessment are not reported in the registry record. These gaps matter when judging how robustly the time-to-event estimate represents the trial data.

11. Confidence Intervals and Precision

The 95% confidence interval for the recalculated primary risk difference runs from -0.042 to -0.006. Because the entire interval is below zero, the posted unadjusted calculation is compatible with a lower event proportion in the rivaroxaban group, while still allowing a range of possible magnitudes. The interval is not a probability statement about the estimate, and it does not incorporate every uncertainty that could arise from missing information or analysis choices.

The sponsor’s time-to-event estimate is a hazard ratio of 0.85, with a 95% confidence interval from 0.76 to 0.96. This interval also lies below 1, the value corresponding to equal hazards under the usual ratio interpretation. It conveys uncertainty around the time-to-event estimate, not around the crude risk difference. The two intervals therefore should be interpreted according to their respective measures.

Precision depends partly on the number of observed events and the amount and distribution of follow-up, as well as on the statistical method. The registry reports a mean follow-up survival time until the efficacy cut-off of 1109.76 days, but does not give the full distribution of follow-up or detailed censoring information. The confidence intervals describe statistical uncertainty conditional on the method and data used; they do not remedy absent details about data handling, outcome adjudication, or the endpoint components.

The interval’s width also matters. A confidence interval that excludes a null value can still include effects of different practical importance. The record does not establish a threshold for clinical importance for the risk difference or hazard ratio. Thus the estimates support a direction and range of statistical effects, but the precision should not be confused with certainty about the clinical meaning of each component or about effects outside the trial population.

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 justification. For these binary participant-outcome calculations, the figures are participants per arm. In general, sample-size displays for time-to-event outcomes give total events instead; that distinction depends on the outcome type and should be kept clear when reading planning results.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The registry record does not report the original trial’s sample-size assumptions or justification, so these calculations should not be treated as a reconstruction of the design used for this trial.

The 80% power column describes the planned number of participants per arm under the assumptions for a design intended to have an 80% chance of detecting the chosen effect if that effect is the true one. The 90% power column describes the corresponding planning target for a 90% chance. These are design concepts, not probabilities that the observed result is correct. Smaller effects require more participants to detect under otherwise unchanged assumptions; the planning rows illustrate that relationship by considering 100%, 75%, and 50% of the observed effect.

This is not observed power. Power is a planning quantity based on assumptions about the effect and design, and calculating it after the result from the observed effect does not add evidence about whether the finding is real. The interpretation should rest on the observed estimates, their confidence intervals, the trial design, and the limits of the registry record, rather than a retrospective power figure.

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 = 0.178; treatment proportion p₁ = 0.155; average p̄ = 0.166.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5267 = 1.0323.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5264 = 0.4430.
4. n = (1.0323 + 0.4430)² / (-0.0236)² = 3,920.5, rounded up to 3,921 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 <- 0.178157413056742                          # control proportion
p1 <- 0.154595252586732                          # 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(2504216)
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 = 3,921 (80% power), 5,248 (90% power)
 75% of observed effect: n per arm = 7,069 (80% power), 9,463 (90% power)
 50% of observed effect: n per arm = 16,127 (80% power), 21,588 (90% power)
power.prop.test: 3920.5 
Simulated power at n = 3,921 per arm: 0.795 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis is a log-rank time-to-event analysis. It gives a hazard ratio of 0.85, a 95% confidence interval from 0.76 to 0.96, and p = 0.004. The registry labels it as a superiority analysis. These are the sponsor’s own reported inferential results for the primary outcome.

The recalculated estimate uses the posted participant counts and group sizes to form an unadjusted risk difference of -0.024, with a 95% confidence interval from -0.042 to -0.006 and p = 0.01. It is a simple summary based on the proportions with an event and does not use event timing in the way the log-rank analysis does. The hazard ratio and risk difference have different scales, so their numerical values cannot be compared directly.

The registry record does not flag a discrepancy between the sponsor’s reported analysis and the recalculation. Their directions are consistent, but the sponsor’s analysis remains the trial’s own time-to-event result and should be distinguished from the supplementary unadjusted re-calculation. The record does not provide enough detail to independently reproduce the sponsor’s full time-to-event analysis, including its handling of censoring and model assumptions.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, comparisons, subgroups, or interim looks. As a general statistical matter, testing many hypotheses can increase the chance of at least one apparently positive result under a setting where all null hypotheses are true. Methods such as a prespecified hierarchy or an adjustment to the testing threshold can address that concern, but the registry record does not report whether such procedures were used for the secondary outcomes.

The record lists multiple secondary outcomes and analyses, but it does not report a multiplicity strategy, a testing hierarchy, or a detailed statistical analysis plan. It also does not report whether interim analyses were planned or conducted. These details are important for judging how confirmatory to regard secondary p-values and whether the primary inference was affected by any repeated testing. Their absence should not be filled in by assumption.

For the primary analysis, the registry identifies the intention-to-treat set as all randomized participants. This is a clear population definition, but it does not answer how missing outcome information was handled, whether all randomized participants had complete follow-up, or how censoring was implemented in the time-to-event analysis. Those details are not reported in the registry record. The primary endpoint description says that the first occurrence after randomization through the efficacy cut-off date was considered, but does not by itself explain the handling of participants without observed events.

Missingness can affect estimates if participants with unavailable outcomes differ systematically from those with observed outcomes. In general, the consequences depend on the amount, timing, and reasons for missing information, and on the method used to address it. No missing-data assumptions or sensitivity analyses are reported in the registry record. As a result, readers cannot assess from this record alone how robust the results are to alternative assumptions about unavailable outcome information.

These omissions do not negate the randomized comparison, but they narrow what can be concluded about the analysis process. They are especially relevant to secondary findings, where multiplicity procedures are not described, and to time-to-event interpretation, where censoring details are unavailable.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0.1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: peripheral arterial occlusive disease (4.0%), intermittent claudication (1.6%), pneumonia (1.4%), peripheral ischaemia (1.0%), postoperative wound infection (0.8%).

The registry reports serious adverse events in 948 of 3256 participants at risk in the rivaroxaban-plus-aspirin group and 927 of 3248 participants at risk in the placebo-plus-aspirin group. It also reports other adverse events in 725 of 3256 participants at risk and 729 of 3248 participants at risk, respectively. These counts describe the registry’s adverse-event summaries; they are not the primary efficacy endpoint and should be read separately from the event-time results.

The listed serious adverse-event terms include peripheral arterial occlusive disease at 4.0%, intermittent claudication at 1.6%, pneumonia at 1.4%, peripheral ischaemia at 1.0%, postoperative wound infection at 0.8%, and peripheral artery stenosis at 0.8%. The registry also records deaths of 327 and 304 in the respective groups. The definitions, adjudication procedures, timing, and causal attribution for these safety summaries are not reported in the registry record. Counts alone do not establish whether an event was caused by assigned treatment or explain the comparative safety profile.

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

The posted primary results show fewer participants with the first composite efficacy event in the rivaroxaban-plus-aspirin group than in the placebo-plus-aspirin group. The sponsor’s time-to-event analysis also reports a hazard ratio below 1, with its 95% confidence interval below 1. These findings describe the randomized comparison for the registry’s defined population, treatment regimens, endpoint, and follow-up window.

The result does not establish that every component of the composite was reduced. Component-specific primary results are not reported in the registry record. It also does not show that the observed pattern applies to people outside the trial population, to other procedures, to other regimens, or to follow-up beyond the efficacy cut-off date. The registry’s mean follow-up survival time of 1109.76 days is a summary, not evidence that each participant was followed for that length of time.

The efficacy comparison also does not settle the interpretation of safety. Serious adverse events, other adverse events, and deaths are reported separately, and counts alone do not establish causation or a complete balance of benefits and harms. The registry does not provide detailed information about adherence, missing-data handling, or the methods used to assess safety events.

Statistical significance is not equivalent to proof, nor does it by itself show that an effect is important to patients. The risk difference and hazard ratio express different aspects of the comparison, and their confidence intervals describe uncertainty under their respective methods. The conclusions should remain tied to those estimates and their limitations. The registry record supports describing the observed direction of the primary comparison, but it does not warrant a claim about every component, every patient, or every clinical setting.

18. Why This Trial Matters Statistically

This trial poses a statistical question in a population where outcomes can occur in more than one vascular territory. Combining cardiovascular and limb events into a primary composite makes an overall comparison possible, but it also creates an interpretation challenge: a single summary can conceal different patterns among its components. Separating what the composite establishes from what remains unknown is central to sound clinical-trial interpretation.

The registry offers two kinds of primary summary. Participant counts and an unadjusted risk difference convey the proportion-level contrast, while the sponsor’s log-rank result uses event timing. Understanding why both can be informative, without treating them as the same measure, is a useful lesson in reading clinical trial results. The confidence intervals also show that statistical estimates are ranges rather than exact descriptions of an underlying effect.

Randomization and an intention-to-treat population strengthen the interpretation of the assigned-group comparison. At the same time, incomplete reporting of missing-data procedures, multiplicity, and time-to-event assumptions limits independent evaluation. Statistical rigor requires recognizing both the design features that support inference and the information gaps that constrain it.

The secondary outcomes illustrate another general issue: a consistent direction across several endpoints can be informative, but unadjusted testing across multiple outcomes requires caution. Distinguishing confirmatory evidence from supportive evidence helps prevent overinterpretation. The trial therefore matters statistically not only for its primary estimate, but also as an example of how endpoint construction, analysis methods, precision, and reporting completeness shape what a result can mean.

19. Limitations

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

The primary endpoint is a composite, and the registry does not report separate primary results for its components. The overall comparison therefore cannot show whether myocardial infarction, ischemic stroke, cardiovascular death, acute limb ischemia, and major amputation each had similar results. Because these events differ in nature, the composite estimate should not be interpreted as a uniform effect across all of them.

The efficacy outcome window ends at 08-Sep-2019, and the record reports a mean time in follow-up survival time until that cut-off of 1109.76 days. The full distribution of follow-up, censoring rules, and time-to-event diagnostics are not reported in the registry record. The reported mean should not be treated as the follow-up duration for every participant.

The record does not report missing-data methods, adherence information, detailed eligibility criteria, or the original sample-size justification. It also does not report a multiplicity plan for secondary outcomes or whether interim analyses occurred. These gaps make it harder to assess robustness, generalizability, and the confirmatory status of secondary findings from the registry record alone.

The secondary results described in the record do not provide detailed numerical information for every listed secondary outcome. Safety reporting gives counts and selected serious adverse-event terms, but the definitions, timing, and causal attribution for those summaries are not reported. Finally, the available results concern the specific aspirin-based comparison after lower-extremity revascularization; they do not establish results for different populations, procedures, or treatment regimens.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Rivaroxaban in Reducing the Risk of Major Thrombotic Vascular Events in Subjects With Symptomatic Peripheral Artery Disease Undergoing Peripheral Revascularization Procedures of the Lower Extremities — NCT02504216.
• Registry record last updated 2020-12-08; status last verified 2020-12.
• Results first posted 2020-12-08.
• 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.

23. Record Summary

NCT02504216 was a completed randomized, quadruple-masked, parallel-group phase 3 trial sponsored by Bayer. It enrolled 6564 participants with symptomatic peripheral artery disease undergoing lower-extremity revascularization. The comparison was rivaroxaban 2.5 mg twice daily plus aspirin 100 mg once daily versus placebo plus aspirin 100 mg once daily.

The primary outcome was the first occurrence of myocardial infarction, ischemic stroke, cardiovascular death, acute limb ischemia, or major amputation due to a vascular etiology. In the intention-to-treat population, the registry reports 508 participants with the outcome in the rivaroxaban group and 584 in the placebo group. The sponsor’s log-rank analysis reports a hazard ratio of 0.85, with a 95% confidence interval from 0.76 to 0.96 and p = 0.004. The registry does not report several analysis details, including missing-data handling and multiplicity procedures.