Ticagrelor With Aspirin or Alone in High-Risk Patients After Coronary Intervention: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ticagrelor With Aspirin or Alone in High-Risk Patients After Coronary Intervention (NCT02270242), a randomized phase 4 study. The primary outcome is Number of Participants With BARC Type 2, 3, or 5.

2. Clinical Question

3. Trial Design

The registry describes a completed, randomized, quadruple-masked, parallel-group Phase 4 trial sponsored by Icahn School of Medicine at Mount Sinai. The recorded study start was 2015-07, and the primary completion date was 2019-07-10. The registry lists enrollment as 9006. The study description says that enrollment occurred at index PCI and that randomization was intended for participants meeting eligibility criteria at 3 months post enrollment. Those randomized were assigned to ticagrelor plus aspirin or ticagrelor plus placebo for an additional 12 months. Follow-up clinic visits were described at 3 months, 9 months, and 15 months post enrollment.

The trial therefore addresses a treatment strategy after coronary intervention, with the randomized comparison beginning after the initial post-enrollment period. Both arms received ticagrelor; the assigned difference was aspirin versus a matching placebo. The registry's masking field is quadruple, but it does not specify in the posted results which roles were masked or how masking was maintained. Allocation is listed as randomized and the model as parallel; details of the random sequence generation and allocation concealment are not reported in the registry record.

The primary results are described for the intention-to-treat population. The posted primary endpoint counts are 141 participants among 3555.0 in the Placebo + Ticagrelor arm and 250 among 3564.0 in the Aspirin + Ticagrelor arm. The ischemic endpoint has separate denominators: 135 among 3524.0 and 137 among 3515.0, respectively. These endpoint-specific denominators should be retained when interpreting each result; the registry does not provide a reconciliation of why the denominators differ.

The brief description refers to up to 9000 subjects, whereas the registry records enrollment of 9006. The registry does not explain that distinction. The original sample-size rationale, the intended power for the trial, and the trial's own statistical analysis plan are not reported in the registry record.

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: 1887 excluded from randomization (106 lost to follow up, 243 had adverse events between enrollment and randomization: a) myocardial infarction, stroke or death, b) revascularizations, and/or c) BARC type 3b or higher bleedings, 1148 were not adherent to DAPT, 267 withdrew consent or declined to participate, and 123 had other reasons.)

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Data for the intention-to-treat population

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 BARC Type 2, 3, or 5, measured over 12 months after randomization.

The primary endpoint counts participants with a first occurrence of clinically relevant bleeding, defined as BARC Type 2, 3, or 5 bleeding, during 12 months after randomization. The registry describes BARC bleeding types as ranging from 0, no bleeding, to 5, fatal bleeding. The endpoint combines the stated BARC categories into a participant-level count rather than reporting the total number of bleeding episodes. A participant with a qualifying first event contributes to the endpoint count.

Using a defined event category and a fixed follow-up timeframe makes the comparison interpretable as the proportion of each randomized group with a qualifying event during the stated period. The clinical rationale in the registry is to assess clinically relevant bleeding while comparing ticagrelor alone with ticagrelor plus aspirin in high-risk patients after intervention. The endpoint is also relevant to the treatment contrast because aspirin is the assigned difference between the arms.

As a general statistical point, a binary participant-level endpoint is straightforward to summarize as an event count and a denominator, and can be compared using risks, risk differences, or relative measures. Such a summary does not convey when events occurred, how many events a participant had after the first event, or the clinical details of each event. The registry record does not report additional analyses of event timing or recurrence.

7. Results Posted in the Registry

• Aspirin + Ticagrelor: 7.0% (250/3564) versus 4.0% (141/3555) on control; risk difference 3.0 percentage points (95% CI 2.0 to 4.1), risk ratio 1.77 (1.45–2.16); 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 Ischemic Episode

• 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:
  • Aspirin + Ticagrelor: 3.9% (137/3515) versus 3.8% (135/3524) on control; risk difference 0.1 percentage points (95% CI -0.8 to 1.0), risk ratio 1.02 (0.81–1.28); unadjusted two-proportion z-test p = 0.885.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aspirin + Ticagrelor and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary endpoint, the number of participants with an ischemic episode during 12 months after randomization. Its group counts are close, and its estimated risk difference is close to zero; the posted interval spans values on both sides of zero. The broad pattern is therefore unlike the primary bleeding result, whose estimate and interval indicate a positive risk difference for the aspirin-containing arm. This comparison of patterns is descriptive and does not by itself establish a trade-off or settle the overall balance of outcomes.

The ischemic endpoint and primary bleeding endpoint are distinct outcomes, each with its own participant counts and denominators. An endpoint may also capture a different clinical process and have a different frequency. A result for one endpoint should not be used as a substitute for another, and the absence of a clear statistical separation on the secondary endpoint does not prove that the groups are identical or that a clinically relevant difference is excluded.

The secondary p-value is unadjusted. As a general statistical concern, multiple endpoint testing increases the chance of a chance-positive finding when results are considered together, unless a testing strategy accounts for the multiplicity. The registry does not report such a strategy. For this reason, unadjusted secondary results generally carry less confirmatory weight than a prespecified primary result, particularly when the analysis plan and hierarchy of tests are unavailable. The registry lists no reported analyses beyond the posted endpoint comparisons.

The secondary result is best read as an additional observation alongside the primary endpoint, rather than as a standalone claim about treatment effects. The record does not report a formal joint assessment of bleeding and ischemic outcomes, a composite balancing the two, or an adjustment that would support stronger conclusions across the set.

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

• Number of Participants With Ischemic Episode

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

The risk difference is the event risk in the comparison arm minus the event risk in the control arm, using the ordering stated in the registry comparison. Here, the comparison is Aspirin + Ticagrelor relative to Placebo + Ticagrelor. A positive risk difference therefore indicates a higher observed event proportion in the aspirin-containing arm. For the primary endpoint, the estimate is 0.030. This is an absolute contrast, not a relative percentage change. It is useful for expressing how far apart the observed risks are on the probability scale.

As a general statistical explanation, an absolute difference is often easier to connect to the frequency of events in the groups than a relative measure. Its interpretation still depends on the endpoint definition, the follow-up period, and the population being analyzed. A risk difference for a fixed timeframe does not describe the timing of events within that timeframe.

How do the relative measures differ?

The risk ratio compares the risk in the aspirin-containing arm with the risk in the placebo arm. The odds ratio compares event odds rather than event risks. Both are relative measures, but odds and risks are not interchangeable. In the primary comparison, the posted risk ratio is 1.769 and the posted odds ratio is 1.827. Each gives a contrast on a different scale; neither replaces the absolute risk difference. The registry lists bounds for both relative measures, but does not describe the methods used to obtain them.

What does the p-value tell the reader?

The primary unadjusted p-value is <0.001, while the secondary unadjusted p-value is 0.885. As a general statistical explanation, a p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A small p-value does not remove uncertainty about the estimate, and a larger p-value does not establish that groups are equivalent.

The registry labels these p-values unadjusted. No multiplicity adjustment is reported. When multiple endpoints or comparisons are examined, unadjusted p-values do not account for the increased chance of at least one seemingly notable result across the set. This is especially relevant when interpreting secondary outcomes, which are not the named primary endpoint.

What is the role of randomization?

As a general principle, random assignment is intended to make treatment groups comparable with respect to both measured and unmeasured baseline factors, on average. That design feature supports interpretation of differences between randomized groups. It does not guarantee identical groups on every characteristic, and it cannot resolve problems such as missing outcome data, deviations from assigned treatment, or incomplete reporting. The registry identifies randomized allocation and an intention-to-treat primary population, but does not report detailed information on these implementation and analysis issues.

Intention-to-treat analysis generally preserves comparison by assigned group, regardless of subsequent treatment adherence, according to the specified analysis plan. The primary endpoint is explicitly described as using the intention-to-treat population. The registry does not provide enough detail to determine how all post-randomization events, unavailable measurements, or protocol deviations were handled. Nor does it post a detailed participant flow accounting for the difference between enrollment and endpoint-specific denominators.

How should the interval estimates be read?

The primary risk-difference interval runs from 0.020 to 0.041, and the secondary interval runs from -0.008 to 0.010. As a general statistical explanation, an interval estimate conveys a range of values reasonably compatible with the data and the method used, subject to the assumptions of that method. It helps show precision and direction more fully than a point estimate alone. The registry does not state the confidence level or the interval-construction method in the posted record, so those details should not be assumed.

For the primary endpoint, both stated bounds are positive. For the ischemic endpoint, the bounds extend across zero, so the interval is compatible with a small difference in either direction. This is a statement about the range of estimates represented by the interval, not proof that all values in it are equally plausible, nor proof of no effect.

What do planning calculations mean?

The posted planning illustrations use the observed effect as a reference and show scenarios for detecting 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Their stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The figures for these binary outcomes are participants per arm. They are planning illustrations based on the observed effect, not a reconstruction of the trial's original design. The original design assumptions and sample-size justification are not reported in the registry record.

As a general statistical principle, smaller target effects are harder to distinguish from random variation at a fixed significance level and power target, so they require more participants under otherwise unchanged assumptions. A planning calculation does not guarantee that a future study will achieve its target power or reproduce the observed effect. It also should not be read as an estimate of power observed after the trial has been completed.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.030, with bounds from 0.020 to 0.041. The interval remains above zero, indicating that the range of values represented by these posted bounds is on the positive side for Aspirin + Ticagrelor relative to Placebo + Ticagrelor. The interval gives more information than the point estimate alone: it shows that the estimated contrast is not known exactly, while keeping the direction consistent across the stated bounds.

The relative estimates are also posted with bounds. The risk ratio is 1.769, with bounds 1.446 and 2.163; the odds ratio is 1.827, with bounds 1.478 and 2.258. These intervals likewise lie above their respective no-contrast value of 1. They express uncertainty on relative scales and should not be mistaken for absolute changes in risk.

For the ischemic endpoint, the risk-difference estimate is 0.001 and its bounds range from -0.008 to 0.010. The interval crosses zero, so the posted data are compatible with an estimate favoring either arm within those bounds. Its width also indicates that the result is not an exact estimate of no difference. The unadjusted p-value of 0.885 is consistent with the lack of a clear separation in this comparison, but it does not establish equivalence.

As a general statistical explanation, interval width reflects precision: narrower intervals indicate less uncertainty on the scale being estimated, while wider intervals indicate more. Precision depends on such factors as event frequency, sample information, and the calculation method. The registry record does not report the confidence level or interval method, so these bounds should be interpreted as posted without assigning an unreported confidence level.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The scenarios use 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect as the effect to detect. These are planning assumptions stated for the illustrations; the original trial design assumptions and sample-size rationale are not reported in the registry record.

The 80% power column gives the estimated participants needed in each arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions are correct. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are prospective design calculations, not descriptions of the completed study's achieved performance.

For the primary endpoint, planning for 100% of the observed effect corresponds to 876 participants per arm for 80% power and 1,172 participants per arm for 90% power. Planning for 75% of the observed effect corresponds to 1,455 and 1,948 participants per arm, respectively. Planning for 50% of the observed effect corresponds to 3,043 and 4,073 participants per arm, respectively. The secondary endpoint has much larger illustrative requirements: 1,310,485 and 1,754,367 participants per arm for 100% of the observed effect; 2,324,926 and 3,112,416 for 75%; and 5,220,226 and 6,988,401 for 50%.

The pattern reflects a general planning principle: smaller effects require more participants to distinguish them from random variation under the same assumptions. These figures are not observed power. They are illustrations calculated from the observed effect, and should not be mistaken for the trial's own prospective sample-size calculation.

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 = 0.040; treatment proportion p₁ = 0.070; average p̄ = 0.055.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3221 = 0.6314.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3214 = 0.2705.
4. n = (0.6314 + 0.2705)² / (0.0305)² = 875.4, rounded up to 876 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 <- 0.039662447257384                          # control proportion
p1 <- 0.0701459034792368                          # 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(2270242)
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 = 876 (80% power), 1,172 (90% power)
 75% of observed effect: n per arm = 1,455 (80% power), 1,948 (90% power)
 50% of observed effect: n per arm = 3,043 (80% power), 4,073 (90% power)
power.prop.test: 875.4 
Simulated power at n = 876 per arm: 0.807 (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 a primary endpoint and posts one secondary endpoint. It gives unadjusted p-values for the posted comparisons, but a multiplicity adjustment or prespecified testing hierarchy is not reported in the registry record. Without that information, the unadjusted secondary result should be treated as exploratory or supportive rather than as a multiplicity-controlled confirmatory finding. The record also does not state whether additional endpoints were measured but not posted.

The primary endpoint population is described as the intention-to-treat population. That identifies the stated analysis population at a high level, but the record does not report detailed analysis rules, handling of protocol deviations, or treatment adherence. The population definition for the secondary endpoint is not reported in the registry record. Endpoint-specific denominators are posted and differ between the primary and secondary comparisons, but a participant flow account explaining those denominators is not reported.

Missing-data methods are not reported in the registry record. In general, unavailable outcome observations can affect estimates if participants with missing data differ systematically from those with observed data. The registry does not say whether missing outcomes were imputed, treated as non-events, excluded, or addressed through sensitivity analyses. It also does not report a detailed account of withdrawal or loss to follow-up relevant to these outcomes.

The registry does not post a statistical analysis plan or describe interim analyses, stopping rules, or adjustment for interim looks. These items should not be inferred from the randomized design or the posted p-values. The registry records no reported analyses in addition to the endpoint comparisons, leaving limited information about robustness checks or adjusted models. Consequently, the posted estimates can be described as reported, but their sensitivity to alternative assumptions and analysis choices cannot be assessed from the registry record.

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 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: barc 235 (7.0%), myocardial infarction (2.8%), stent thrombosis, definite or probable (0.6%), ischemic stroke (0.5%).

The registry lists serious adverse events by randomized group. In Placebo + Ticagrelor, 262 participants are listed as affected among 3555 at risk; in Aspirin + Ticagrelor, 370 are listed as affected among 3564 at risk. Deaths are listed as 34 and 45, respectively. The registry also records zero other adverse events in each group. These figures should be read as registry counts, not as adjusted comparisons or proof that treatment caused the events.

The record lists BARC 235 at 7.0%, Myocardial Infarction at 2.8%, Stent Thrombosis, definite or probable at 0.6%, and Ischemic Stroke at 0.5% among the top serious event terms. The registry does not specify in this listing whether these percentages apply to each arm or provide further detail about the calculation, so they should not be assigned to a particular group.

Serious adverse event summaries are distinct from the primary endpoint analysis. The primary endpoint uses a defined first occurrence of BARC Type 2, 3, or 5 bleeding during 12 months after randomization; the safety listing is a separate registry summary. The record does not provide an adjusted safety comparison or enough detail to interpret these counts as causal effects.

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

The posted primary result shows a higher observed proportion with the defined clinically relevant bleeding endpoint in the Aspirin + Ticagrelor group than in the Placebo + Ticagrelor group. The risk difference is 0.030, and the posted interval runs from 0.020 to 0.041. The unadjusted p-value is <0.001. These statistics describe the randomized-group comparison in the posted intention-to-treat results; they do not establish a mechanism or guarantee the same result in other populations, settings, or follow-up periods.

The ischemic endpoint result is different in pattern: its estimate is 0.001, with bounds from -0.008 to 0.010 and an unadjusted p-value of 0.885. It does not show a clear separation between groups in the posted analysis, but it does not prove identical risks, establish equivalence, or rule out differences within the interval. No equivalence or noninferiority margin is reported.

The comparison is specifically ticagrelor with aspirin versus ticagrelor with placebo after randomization among eligible high-risk patients following PCI with at least one drug-eluting stent. It does not compare ticagrelor against no treatment, nor does it address every possible antiplatelet strategy. The registry's description of high-risk criteria is broad and does not list the qualifying clinical or anatomic conditions.

Statistical significance is not a measure of clinical importance, and a p-value is not the probability that a result is true. The absolute and relative estimates, their uncertainty, endpoint definitions, and population all matter. The posted data do not by themselves determine the clinical importance of the observed contrasts. They also do not provide a formal assessment combining bleeding, ischemic episodes, deaths, and other adverse events.

The findings should therefore be understood as estimates from a completed randomized trial with specific endpoints and a defined follow-up period. Missing-data procedures, multiplicity strategy, detailed analysis methods, and the original sample-size justification are not reported in the registry record. Those gaps limit how fully the results can be independently evaluated.

17. Why This Trial Matters Statistically

This trial is statistically informative because it compares two regimens that share ticagrelor and differ by aspirin versus placebo. That structure focuses the randomized contrast on the addition of aspirin within the study's treatment strategy. Randomization supports a direct comparison between assigned groups, while the intention-to-treat designation for the primary endpoint indicates that the primary result is framed by randomized assignment.

The registry posts an absolute risk difference as well as relative measures for the primary endpoint. This is useful because effect measures answer different questions: an absolute difference describes separation in event probability, while relative measures express the contrast proportionally. Reading these scales together avoids relying on a single summary that might obscure the baseline event frequency or the size of the absolute contrast.

The contrasting pattern across the primary bleeding and secondary ischemic endpoints also illustrates why outcomes must be interpreted separately. The primary estimate is more clearly separated from zero than the secondary estimate, whose interval includes zero. That contrast does not amount to a formal combined benefit-harm analysis, but it shows why multiple outcomes and their uncertainty matter when interpreting a treatment comparison.

The record also makes visible the distinction between observed trial results and planning illustrations. Sample-size scenarios based on the observed effects can help readers understand how assumptions about target effect and desired power change planning requirements. They are not evidence of the trial's original design rationale or its achieved power. Separating prospective planning from post-trial inference is important for sound statistical interpretation.

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 leaves important trial and analysis details unspecified. It does not report the original sample-size justification, the trial's prospective power assumptions, or a detailed statistical analysis plan. The masking field is quadruple, but the roles masked and procedures used to maintain masking are not described in the posted results. Randomization sequence generation and allocation concealment are also not reported.

The registry reports enrollment of 9006, while the brief description says up to 9000 subjects would be enrolled; it does not explain the distinction. The endpoint-specific denominators differ, and the record does not provide a participant flow account or reasons for those differences. Missing outcome data and their handling are not reported, nor are withdrawal, treatment adherence, or sensitivity analyses described in sufficient detail.

The primary endpoint has a stated intention-to-treat population, but the corresponding population definition for the secondary result is not reported in the registry record. The posted p-values are unadjusted, and no multiplicity plan or hierarchy of testing is stated. Consequently, the secondary result has limited confirmatory interpretation, and the record does not permit assessment of whether conclusions are robust to alternative missing-data or testing assumptions.

The eligibility description defines high risk only in broad terms, referring to clinical and/or anatomic criteria. Specific criteria are not listed. The record describes follow-up and endpoint timing, but does not post detailed event adjudication procedures or a full account of the statistical methods used for interval estimates. These reporting limitations constrain reproducibility and the assessment of how broadly the observed findings apply.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Ticagrelor With Aspirin or Alone in High-Risk Patients After Coronary Intervention — NCT02270242.
• Registry record last updated 2021-01-13; status last verified 2020-12.
• Results first posted 2020-08-19.
• 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

NCT02270242 is a completed randomized, quadruple-masked, parallel-group Phase 4 trial sponsored by Icahn School of Medicine at Mount Sinai. It compared ticagrelor plus aspirin with ticagrelor plus placebo in high-risk patients after PCI with at least one drug-eluting stent. The registry records enrollment of 9006 and primary completion on 2019-07-10.

The primary endpoint was the number of participants with a first BARC Type 2, 3, or 5 bleeding event during 12 months after randomization, in the intention-to-treat population. The posted risk difference was 0.030, with bounds from 0.020 to 0.041 and an unadjusted p-value of <0.001. The secondary ischemic endpoint had a risk difference of 0.001, with bounds from -0.008 to 0.010 and an unadjusted p-value of 0.885.

The registry does not report the original sample-size rationale, detailed missing-data methods, or multiplicity strategy. Planning illustrations are based on observed effects and should not be interpreted as observed power.