Antiplatelet Strategy for Peripheral Arterial Interventions for Revascularization of Lower Extremities: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Antiplatelet Strategy for Peripheral Arterial Interventions for Revascularization of Lower Extremities (NCT02217501), a randomized phase 3 study. The primary outcome is Number of Participants With First Occurrence of Target Vessel Occlusion, Surgical Revascularization, Endovascular Revascularization, Major Amputation of Target Limb, Ischemic Stroke, MI, or Death.

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, parallel-group trial with no masking. It was sponsored by the University of Texas Southwestern Medical Center and is recorded as completed. The registry lists enrollment of 159. The study began in 2015-11, and primary completion is recorded as 2020-01-30. These are registry dates; they do not, by themselves, describe how long individual participants were followed.

The comparison assigned participants to one of two dual antiplatelet therapy durations after endovascular treatment for peripheral arterial disease. Both groups were prescribed clopidogrel 75 mg daily and ASA 75-100 mg daily. One group continued treatment for the clinically indicated duration plus an additional 12 months. The other followed the clinically indicated duration, with a minimum of 30 days. Thus, the randomized contrast was duration of the combined regimen rather than a comparison of different medicines.

Because masking was listed as none, the trial was open-label. This describes knowledge of assignment, not whether outcome assessors were blinded; that detail is not reported in the registry record. The record also does not report the method used to generate or conceal the random allocation, whether randomization was stratified, or the planned analysis population. Original sample-size assumptions and the protocol's statistical plan are not reported in the registry record. The posted enrollment should therefore be read as the trial's recorded enrollment, not as evidence of how the original target was chosen.

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

Reasons for not completing this period:

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With First Occurrence of Target Vessel Occlusion, Surgical Revascularization, Endovascular Revascularization, Major Amputation of Target Limb, Ischemic Stroke, MI, or Death, measured over 12 months from index procedure or end of study treatment, whichever is longer, assessed up to 2 years.

The primary endpoint counts participants with a first occurrence of a composite event. Its listed components are target-vessel occlusion, surgical revascularization, endovascular revascularization, major amputation of the target limb, ischemic stroke, myocardial infarction, or death. The registry describes occlusion as documented by an imaging procedure, including duplex ultrasonography, at a follow-up visit within the stated outcome period. The recorded timeframe is 12 months from the index procedure or the end of study treatment, whichever is longer, assessed up to 2 years.

A composite endpoint can capture several clinically important kinds of events in one outcome measure. In general, this can make a trial-level comparison more informative when individual components occur infrequently, but it also means the combined result does not show which component primarily shaped the estimate. The registry posts the number of participants with the composite outcome; separate primary-endpoint counts for each component are not reported in the registry record. The posted measure is a participant count, not a count of every event or a time-to-event estimate. The registry record does not provide further detail on adjudication procedures or how a first occurrence was determined when more than one component was relevant.

7. Results Posted in the Registry

• DAPT - Clinically Indicated Duration: 19.5% (16/82) versus 16.9% (13/77) on control; risk difference 2.6 percentage points (95% CI -9.4 to 14.6), risk ratio 1.16 (0.60–2.24); unadjusted two-proportion z-test p = 0.668.

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 First Occurrence of 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:
  • DAPT - Clinically Indicated Duration: 4.9% (4/82) versus 6.5% (5/77) on control; risk difference -1.6 percentage points (95% CI -8.8 to 5.6), risk ratio 0.75 (0.21–2.70); unadjusted two-proportion z-test p = 0.660.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DAPT - Clinically Indicated Duration and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome, first occurrence of bleeding. Its results offer a separate safety-related view alongside the primary composite, which includes vascular, limb, and mortality events. The secondary endpoint is not a component-by-component explanation of the primary result, and it cannot establish why the primary group estimates differed. It addresses a different event definition and should be interpreted on its own terms.

For the bleeding analysis, the registry reports a Cochran-Mantel-Haenszel p-value of 0.659. The simple unadjusted comparison also has a confidence interval that includes no difference. Neither result provides strong statistical evidence of a difference, but neither establishes that the groups have identical bleeding risks. The estimates are based on few recorded bleeding events, which limits precision. The registry does not post a confidence interval for its named Cochran-Mantel-Haenszel analysis.

Secondary outcomes generally carry less confirmatory weight than a prespecified primary outcome because there may be several opportunities to find an apparently notable result when many outcomes are examined. That concern is often addressed by a planned multiplicity strategy. The registry record does not report whether a multiplicity adjustment was planned or applied. With only one secondary outcome posted, the record still does not establish whether other outcomes were considered in the analysis plan or whether all planned results were reported.

The secondary finding should therefore be treated as supportive descriptive evidence, not as a substitute for the primary comparison or as definitive evidence about bleeding. The registry record does not provide enough detail to determine the exact role assigned to this secondary endpoint in the original statistical plan.

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

• Number of Participants With First Occurrence of Bleeding

9. Statistical Interpretation

10. Statistical Methods Explained

What kind of outcome is being compared?

The primary measure is binary at the participant level: each participant either had a recorded first occurrence of the composite outcome during the specified timeframe or did not. The posted group results are counts of participants with an event and the corresponding group sizes. This is different from counting every event, since one participant may experience more than one component or event over follow-up. The registry reports the endpoint as a count of participants, and does not post separate primary component counts.

For a binary outcome, a group risk is the proportion of participants in that group who experienced the outcome. The posted comparison uses 0.169 for the extended-duration group and 0.195 for the clinically indicated-duration group. These are the risks used in the unadjusted two-group comparison. The risk difference subtracts one group's risk from the other's; its sign depends on the stated comparison order. Here, the comparison is clinically indicated duration relative to extended duration, and the reported estimate is 0.026. The result is an absolute contrast, rather than a relative percentage change.

How should the risk difference be read?

A risk difference of zero is the reference for no absolute difference between groups. Positive values in this comparison indicate a higher observed risk in the clinically indicated-duration group; negative values indicate a lower observed risk in that group. This direction describes the coding of the contrast, not whether the difference is clinically important. The confidence interval ranges from -0.093 to 0.146, so the estimate allows for differences in either direction as well as values near zero.

What do relative risk and odds ratio add?

The reported relative risk is 1.156, with a confidence interval from 0.596 to 2.242. It compares the event risks as a ratio. A value of 1 is the reference for equal risks. The reported odds ratio is 1.193, with a confidence interval from 0.532 to 2.679; an odds ratio of 1 is the reference for equal odds. Both intervals include their no-difference reference value. Relative risk and odds ratio use different scales and should not be treated as interchangeable, especially when outcomes are not rare. In this trial, they are complementary descriptions of the same binary comparison rather than separate tests or separate outcomes.

What does a p-value assess?

The unadjusted primary comparison has a p-value of 0.668. In general, a p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions held. It does not give the probability that the null model is true, and it does not indicate the probability that a treatment effect is clinically important. A p-value should be considered alongside the point estimate, its uncertainty, the outcome definition, and the design. The primary analysis method and any covariate adjustment are not reported in the registry record; the posted comparison is identified as unadjusted.

What analysis method is reported for bleeding?

For the secondary bleeding outcome, the registry lists a Cochran-Mantel-Haenszel analysis and a reported p-value of 0.659. In general, the Cochran-Mantel-Haenszel method can combine evidence across strata to account for a stratification factor or factors. The registry record does not identify the strata or explain how that method was implemented. It also does not provide a reported effect estimate or confidence interval for that analysis. The separate simple unadjusted recalculation for the binary outcome should not be confused with the named registry analysis.

Only one secondary outcome is posted: first occurrence of bleeding. The presence of a named analysis for that outcome does not reveal whether other analyses were planned, whether the endpoint was prespecified in the final protocol, or how results were selected for posting. Those details are not reported in the registry record.

What assumptions matter for these methods?

General statistical interpretation of a two-group binary comparison relies on the outcome being classified consistently and on the analysis representing the randomized groups as intended. The registry record does not report how missing outcome information was handled, whether participants were analyzed according to random assignment, or whether any participants changed treatment. It also does not describe the event-adjudication process, the handling of events outside the specified follow-up window, or methods for addressing variation in follow-up. These omissions limit what can be inferred about implementation of the analysis.

Confidence intervals and p-values quantify sampling uncertainty under their statistical assumptions; they do not account automatically for possible bias from incomplete follow-up, outcome classification, or departures from the planned analysis. The open-label design is a design feature, but its potential influence depends on how outcomes were assessed and managed. Those specific procedures are not reported in the registry record. Accordingly, the posted binary estimates are useful summaries of the recorded comparisons, while the record does not contain enough detail to reconstruct the full primary statistical analysis.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.026, and its 95% confidence interval ranges from -0.093 to 0.146. The interval crosses zero, the reference value for no absolute difference. It also reaches both negative and positive values, so the result does not pin down the direction of the underlying difference with precision. The reported relative-risk interval, 0.596 to 2.242, and odds-ratio interval, 0.532 to 2.679, likewise include their respective no-difference values.

In general, a confidence interval describes a range of estimates compatible with the observed data and the method's assumptions. It is not a range containing a known proportion of individual participant outcomes, nor is it the probability that the true effect lies within the particular interval. Wider intervals indicate less precision than narrower intervals on the same scale. The primary interval is broad enough to include materially different directions and magnitudes of association, so the point estimate alone should not be treated as a settled estimate of the effect.

The recorded event counts are limited, and the registry reports no separate primary estimates for the components of the composite. Thus, neither precision for individual components nor precision for differences in particular kinds of events can be assessed from the posted primary result. The interval also reflects only the statistical calculation; it cannot address possible uncertainty from unreported analysis choices, missing data, or outcome assessment. The registry record does not report adjusted confidence intervals or a primary analysis method that would permit comparison with the unadjusted estimate.

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, rather than the trial's original design calculations. Because the outcomes are binary and the planning information specifies participants per arm, the entries refer to participants per arm, not total events. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculation varies the effect to detect by using the stated fraction of the observed effect.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect and the model assumptions were correct. The 90% power column uses a higher target chance of detection, so its corresponding planning requirement is larger. These are design-planning quantities, not a measure of how likely the observed result was to be correct.

Rows describing planning for 100% of the observed effect use the observed effect as the target; the 75% and 50% rows use progressively smaller target effects. Smaller effects are harder to distinguish from random variation, so the corresponding planning figures require more participants per arm. The exact entries differ by endpoint and are displayed with the relevant planning results. The plotted curve should be read as illustrating how the required planning size changes with the target effect, not as additional observed trial data. These calculations are not observed power. The registry record does not report the trial's original sample-size justification or original design assumptions.

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 = 0.169; treatment proportion p₁ = 0.195; average p̄ = 0.182.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5456 = 1.0694.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5453 = 0.4590.
4. n = (1.0694 + 0.4590)² / (0.0263)² = 3,379.6, rounded up to 3,380 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 <- 0.168831168831169                          # control proportion
p1 <- 0.195121951219512                          # 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(2217501)
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 = 3,380 (80% power), 4,524 (90% power)
 75% of observed effect: n per arm = 5,925 (80% power), 7,931 (90% power)
 50% of observed effect: n per arm = 13,139 (80% power), 17,588 (90% power)
power.prop.test: 3379.6 
Simulated power at n = 3,380 per arm: 0.801 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and posts one secondary outcome, first occurrence of bleeding. It reports a single analysis for the posted secondary outcome using the Cochran-Mantel-Haenszel method. The record does not describe a family of planned hypotheses, a hierarchy of endpoints, or a procedure for controlling the chance of false-positive findings across multiple analyses. Whether a multiplicity strategy was specified or applied is not reported in the registry record.

The analysis population is also not described. The record does not state whether the primary comparison followed intention-to-treat principles, whether participants were analyzed as randomized, or whether a per-protocol or other population was used. It does not report participant flow by analysis set, missing outcome counts, reasons for missingness, or methods used to handle missing data. No conclusion about complete follow-up or absence of missing data can be drawn from the posted results alone.

Interim analyses, stopping rules, and any associated adjustment to statistical thresholds are not reported in the registry record. The original primary statistical method, any covariate adjustment, and the prespecified handling of the composite endpoint are also not reported. The secondary method is named, but its strata and implementation are not specified. These gaps mean the posted estimates can be interpreted as reported comparisons, but the full inferential framework cannot be reconstructed.

In general, multiplicity matters because repeated testing can increase the chance of at least one apparently unusual result under a collection of no-effect hypotheses. Missing-data methods matter because conclusions can depend on how unavailable outcomes are treated, particularly if missingness is related to prognosis or treatment. These are general statistical considerations; the registry record does not indicate which, if any, such issues arose in this trial or how they were addressed.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: repeat endovascular revascularization (19.5%), amputation (14.6%), bleeding (3.9%), myocardial infarction (3.7%), bleeding requiring transfusion (2.6%).

The serious adverse event record lists 27 affected participants among 77 at risk in the extended-duration group and 37 among 82 at risk in the clinically indicated-duration group. It lists 3 deaths in the former group and 4 in the latter. The record separately lists 1 other adverse event in each group. These are descriptive safety counts and are not, by themselves, estimates of treatment-caused harm. In an open-label randomized trial, interpretation still depends on how events were collected, classified, and attributed; those procedures are not reported in the registry record.

The listed serious adverse-event terms include repeat endovascular revascularization at 19.5%, amputation at 14.6%, bleeding at 3.9%, myocardial infarction at 3.7%, bleeding requiring transfusion at 2.6%, and stroke at 2.4%. These are the registry's listed percentages. The record does not make clear whether categories overlap, so the percentages should not be added or treated as mutually exclusive. Nor does the list establish that an event was caused by the assigned regimen.

The separately posted secondary bleeding outcome uses its own endpoint definition and analysis. It should not be assumed to match every adverse-event term labeled bleeding. The record does not report additional details needed to reconcile those measures.

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

The trial compares assignment to extended dual antiplatelet therapy with assignment to a clinically indicated duration after endovascular treatment for peripheral arterial disease. The posted primary estimate is an unadjusted comparison of participants with a composite outcome. Its confidence interval includes no difference and values on both sides of that reference. The results therefore do not provide a precise estimate of the direction or size of the group contrast.

These data do not establish that extending treatment reduces the composite outcome, and they do not establish that it increases the outcome. They also do not establish equivalence or prove that any difference is absent. A conclusion of equivalence would require an appropriate design and a prespecified margin, neither of which is reported in the registry record. A non-significant p-value alone cannot support that conclusion.

The composite combines occlusion, revascularization, amputation, stroke, myocardial infarction, and death. The posted count cannot tell readers whether the event pattern was consistent across components. The registry does not provide separate primary component results or a detailed account of outcome adjudication. The bleeding result is a separate secondary outcome and also does not resolve the primary comparison.

Interpretation is further bounded by the information available about analysis and follow-up. The record does not report missing-data handling, the primary analysis method, the analysis population, or the original statistical plan. These omissions do not invalidate the posted counts, but they limit assessment of how robust the comparison is to analysis decisions. The open-label design is recorded; details about blinded outcome assessment are not.

The appropriate statistical reading is that the registry reports an inconclusive comparison with substantial uncertainty, not a definitive verdict for either duration. The results describe the participants and outcomes recorded in this trial. They do not by themselves settle how the strategies compare in other populations, settings, or treatment protocols.

17. Why This Trial Matters Statistically

This trial illustrates why a difference in observed event counts is not enough to establish a dependable treatment contrast. The primary outcome counts are numerically different between groups, but the unadjusted risk-difference interval spans negative and positive values and includes zero. Considering the estimate together with its uncertainty prevents a directional point estimate from being mistaken for a conclusive result.

The endpoint is a composite of several clinically distinct outcomes. Combining components can make an overall comparison possible when events are uncommon, but it also makes the aggregate result harder to interpret without component-specific estimates. In this record, separate primary component counts are not reported. The overall estimate therefore cannot show whether one component contributed most to the observed pattern or whether component effects differed.

The trial also demonstrates the distinction between the result of a study and a design-planning illustration. The posted planning figures use the observed effect and specified assumptions; they are not the trial's original sample-size rationale and cannot be read as observed power. A planning exercise is sensitive to the effect targeted, and smaller effects require larger planned group sizes. The original design assumptions are not reported in the registry record.

Finally, a randomized design is important for comparing assigned strategies, but a complete statistical interpretation also depends on analysis populations, missing-data handling, endpoint procedures, and multiplicity plans. Those details are not available in the registry record. Clear reporting of both estimates and methods is essential to distinguish what the posted results support from what remains uncertain.

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 enrollment was 159, and the primary outcome counts were 13 and 16. These recorded numbers indicate that the comparison rests on a limited number of composite events, which is consistent with the broad confidence interval. The primary endpoint combines outcomes that may differ in frequency and clinical meaning, but the registry does not post separate primary results for its components. This prevents assessment of whether the overall estimate represents a consistent pattern across the endpoint.

The trial was open-label. The registry record does not say whether outcome assessors were blinded or how event adjudication was conducted. That missing detail matters for assessing possible influence of knowledge of assignment on event ascertainment, particularly for outcomes involving clinical decisions such as revascularization. The record does not establish that such influence occurred; it simply does not provide enough information to evaluate it.

The outcome timeframe extends to 12 months from the index procedure or the end of study treatment, whichever is longer, assessed up to 2 years. Because the assigned durations differ, the treatment-period rule could result in differences in the time over which participants were observed. The registry does not report detailed follow-up distributions, missing outcome information, or how variable follow-up was handled analytically.

Further limitations are the absence of the original primary analysis method, analysis population, missing-data procedures, interim-analysis information, and multiplicity plan. The criteria for clinically indicated treatment duration are also not reported. These uncertainties restrict evaluation of treatment adherence, protocol implementation, and analysis robustness. The posted results remain interpretable as registry-reported group comparisons, but the record does not contain enough methodological detail for a full audit of the trial analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Antiplatelet Strategy for Peripheral Arterial Interventions for Revascularization of Lower Extremities — NCT02217501.
• Registry record last updated 2021-02-21; status last verified 2021-02.
• Results first posted 2021-02-21.
• 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

NCT02217501 is a completed, randomized, open-label, parallel-group phase 3 trial sponsored by the University of Texas Southwestern Medical Center. It studied clopidogrel and ASA for clinically indicated duration with or without an additional 12 months in people receiving endovascular treatment for peripheral arterial disease. Enrollment was 159.

The primary endpoint was the number of participants with a first occurrence of target-vessel occlusion, revascularization, major amputation of the target limb, ischemic stroke, myocardial infarction, or death. The unadjusted risk difference for clinically indicated duration relative to extended duration was 0.026, with a 95% confidence interval from -0.093 to 0.146 and an unadjusted p-value of 0.668. The interval includes no difference and allows for effects in either direction.

Bleeding was the one posted secondary outcome. The registry record does not report the original primary analysis method, sample-size rationale, analysis population, missing-data approach, or multiplicity plan. The posted results are therefore best interpreted as an uncertain comparison rather than a definitive conclusion about the relative effects of the assigned durations.