A Clinical Trial to Demonstrate the Efficacy of Cangrelor: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Clinical Trial to Demonstrate the Efficacy of Cangrelor (NCT00305162), a randomized phase 3 study. The primary outcome is Incidence of All-cause Mortality, Myocardial Infarction (MI), and Ischemia-driven Revascularization (IDR).

2. Clinical Question

3. Trial Design

This was a randomized phase 3, parallel-group trial with triple masking. Its official title describes a comparison of cangrelor and clopidogrel in subjects requiring PCI. The listed conditions are myocardial infarction (MI) and acute coronary syndromes (ACS). The registry record lists enrollment as 8882, a start date of 2006-04, primary completion in 2009-05, and status as terminated. A reason for termination is not reported in the registry record.

The cangrelor arm description specifies matching placebo capsules, a cangrelor bolus of 30 mcg/kg, and infusion of 4 mcg/kg/min, followed by active clopidogrel 600mg. The infusion was described as running from randomization for at least 2 hours, or until the end of PCI if that was longer, with the option to extend up to 4 hours maximum at investigator discretion. The clopidogrel arm description specifies clopidogrel capsules 600 mg, matching placebo bolus and infusion, and matching placebo capsules after infusion. These are the treatment descriptions in the registry; other treatment procedures are not reported in the registry record.

The primary endpoint population is identified as mITT, excluding STEMI. The endpoint counts participants with the composite outcome from randomization through 48 hours after randomization. The primary endpoint denominators are 3889.0 for cangrelor and 3865.0 for clopidogrel. The safety record uses different at-risk counts, and the registry record does not explain the population definitions or the difference in denominators. Details such as the randomization procedure, allocation concealment, masking roles, and the original statistical design assumptions 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.

48 Hour Follow-up Period

30-day Follow-up Period

1 Year Follow-up Period

Analysis population for the primary outcome, as defined in the registry: mITT (excluding STEMI)

5. Baseline Characteristics

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

Population: Intent-to-treat (ITT) population

6. Primary Endpoint

The registry lists the primary outcome as Incidence of All-cause Mortality, Myocardial Infarction (MI), and Ischemia-driven Revascularization (IDR), measured over randomization through 48 hours after randomization.

The primary endpoint is the incidence of all-cause mortality, myocardial infarction (MI), or ischemia-driven revascularization (IDR), treated as a composite outcome. It counts participants in the mITT population, excluding STEMI, with an event from randomization through 48 hours after randomization. The posted counts are 290.0 of 3889.0 in the cangrelor arm and 276.0 of 3865.0 in the clopidogrel arm.

A composite combines several clinically distinct event types into one endpoint. In general, this can capture whether a participant experienced any component in the specified period and can provide a broader measure of early events than considering a single component alone. It also means that the total composite result does not, by itself, show which component contributed most to the difference or whether components moved in the same direction. The registry record identifies the composite incidence, but does not report further details about event adjudication or how multiple components in one participant were handled.

The chosen timeframe is short and begins at randomization. Interpretation therefore concerns events recorded within that stated interval, not outcomes over an unreported longer follow-up period. The registry record states that the study objective was to demonstrate superiority or at least non-inferiority, but a non-inferiority margin and the formal testing procedure are not reported in the registry record.

7. Results Posted in the Registry

• Clopidogrel Arm: 7.1% (276/3865) versus 7.5% (290/3889) on control; risk difference -0.3 percentage points (95% CI -1.5 to 0.8), risk ratio 0.96 (0.82–1.12); unadjusted two-proportion z-test p = 0.593.

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.

Incidence of All-cause Mortality and MI

• 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:
  • Clopidogrel Arm: 6.8% (261/3865) versus 7.3% (285/3889) on control; risk difference -0.6 percentage points (95% CI -1.7 to 0.6), risk ratio 0.92 (0.78–1.08); unadjusted two-proportion z-test p = 0.322.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Clopidogrel Arm and the control. The interval gives the range of effects that remain compatible with the data.

Individual Incidence of All-cause Mortality

• 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:
  • Clopidogrel Arm: 0.1% (5/3865) versus 0.2% (8/3889) on control; risk difference -0.1 percentage points (95% CI -0.3 to 0.1), risk ratio 0.63 (0.21–1.92); unadjusted two-proportion z-test p = 0.411.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Clopidogrel Arm and the control. The interval gives the range of effects that remain compatible with the data.

Individual Incidence of IDR

• 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:
  • Clopidogrel Arm: 0.6% (23/3865) versus 0.3% (13/3889) on control; risk difference 0.3 percentage points (95% CI -0.0 to 0.6), risk ratio 1.78 (0.90–3.51); unadjusted two-proportion z-test p = 0.091.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Clopidogrel Arm and the control. The interval gives the range of effects that remain compatible with the data.

The registry record lists a range of secondary outcomes, including combinations and individual components involving mortality, MI, IDR, stroke, and procedural complications. The posted secondary results include counts and unadjusted comparisons for all-cause mortality and MI together, all-cause mortality alone, and IDR alone. These outcomes relate to the primary composite because some are components of, or closely overlap with, the primary endpoint. They provide additional descriptions of outcome patterns, but they do not replace the primary comparison.

Across the posted secondary comparisons, the estimates do not provide a consistent, precise basis for claiming a treatment difference. The individual comparisons have uncertainty, and their interpretation should take account of the number of outcomes examined. The primary result remains the central registry outcome: the secondary findings cannot be used to select a favorable component after seeing the data and then treat it as if it had been the sole prespecified question.

The posted secondary p-values are unadjusted. When many outcomes are tested, the chance of at least one apparently notable result can increase, even if there is no underlying difference for any outcome. Adjustment methods or a hierarchical testing plan can address some of this issue, but a multiplicity procedure is not reported in the registry record. Unadjusted secondary findings therefore carry less weight than a prespecified primary analysis and should generally be considered exploratory rather than confirmatory.

The registry lists 17 outcome measures and 16 posted secondary outcomes. No reported secondary analysis entries are listed. The record does not state how outcomes were prioritized, whether all planned outcomes were reported, or how missing outcome data were handled. The secondary results are most useful as context for the primary composite and as descriptions of the recorded endpoints; they do not establish separate treatment effects or resolve the limitations of the primary inference.

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

• Incidence of All-cause Mortality and MI
• Individual Incidence of All-cause Mortality
• Individual Incidence of IDR
• Incidence of Stroke
• Incidence of Abrupt Closure, Threatened Abrupt Closure, Need for Urgent Coronary Artery Bypass Graft (CABG) Surgery, or Unsuccessful Procedure During the Index PCI
• Incidence of All-cause Mortality, MI or IDR
• Incidence of All-cause Mortality or MI
• Incidence of All-cause Mortality

9. Statistical Interpretation

10. Statistical Methods Explained

What does the event count represent?

The primary endpoint is binary at the participant level: a participant is counted as having the composite outcome if the endpoint definition is met during the stated interval. The posted values are counts of participants with events, rather than event rates per unit of follow-up time. The denominator is the number of participants in each arm used for this endpoint. The registry identifies the analysis population as mITT, excluding STEMI, and gives the endpoint-specific denominators as 3889.0 and 3865.0.

A composite endpoint groups multiple outcomes together. That approach answers whether a participant had any of the listed outcomes, but it does not make the components interchangeable in importance or frequency. The aggregate result cannot identify the contribution of each component. The registry record lists additional outcomes, but detailed event-adjudication methods and component-priority rules are not reported in the registry record.

How should the risk difference be read?

The risk difference compares the event proportions between arms on an absolute scale. The posted direction is clopidogrel minus cangrelor, so a negative estimate points toward a lower observed event proportion in the clopidogrel arm; a positive estimate would point in the other direction. The primary estimate is -0.003. Its confidence interval, -0.015 to 0.008, crosses the no-difference point. This means the data do not pin down the direction of the underlying difference with precision sufficient to exclude either direction.

The posted proportions, 0.075 and 0.071, are the observed arm-specific event proportions. They are not adjusted for other characteristics in the posted comparison. The registry record does not report an adjusted primary analysis, covariate adjustment, or a detailed model specification.

What do the relative measures add?

The registry also posts relative risk and odds ratio summaries. Relative measures compare the event frequency across arms as a ratio rather than as an absolute difference. The posted relative risk is 0.958, with a confidence interval from 0.817 to 1.122; the posted odds ratio is 0.954, with a confidence interval from 0.804 to 1.133. Both intervals span their respective no-association values, so neither summary resolves the uncertainty about direction. These relative measures use the same binary endpoint and should not be read as independent replications of the primary result.

What does the p-value say?

The posted unadjusted p-value is 0.593. In general, a p-value measures how unusual data at least as inconsistent with a specified null hypothesis would be if that null model and the test assumptions held. It is not an effect size, and it does not measure the probability that the null hypothesis is true. The registry record does not report a full description of the test, its assumptions, or a prespecified analysis plan. The p-value should therefore be read alongside the observed estimate and confidence interval, not as a stand-alone verdict.

What is not established by the posted methods?

The registry record states a goal of superiority or at least non-inferiority, but does not report the non-inferiority margin, the type I error allocation, the formal primary testing sequence, or the precise analysis procedure for that objective. It also does not report interim analyses, missing-data handling, or a plan for multiplicity across outcomes. Those omissions matter because a statistical claim depends not only on the observed estimate, but also on the prespecified hypothesis, analysis population, assumptions, and decision rule.

Randomization supports a comparison between assigned arms in principle, while masking can reduce some forms of bias in treatment delivery and outcome assessment. The registry labels the study randomized and triple-masked, but details of implementation are not reported in the registry record. The posted endpoint numbers alone cannot verify those procedures or establish whether all participants were analyzed according to the original assignment.

11. Confidence Intervals and Precision

A confidence interval describes a range of effect estimates compatible with the observed data under the statistical method used. It conveys precision as well as direction: a narrower interval indicates less uncertainty about the estimate, while a wider interval leaves more plausible values. The primary risk difference is -0.003, with a 95% confidence interval from -0.015 to 0.008. Because this interval crosses the no-difference point, it does not exclude either direction of difference.

The interval should be interpreted on the absolute risk-difference scale and with the stated comparison direction, clopidogrel minus cangrelor. Its negative values are compatible with a lower event proportion in the clopidogrel arm, while its positive values are compatible with a lower event proportion in the cangrelor arm. The point estimate lies within that range, but the range is more informative about uncertainty than the point estimate alone.

The relative risk interval, 0.817 to 1.122, also spans the no-association value for a ratio. The odds ratio interval, 0.804 to 1.133, does so as well. Relative and absolute scales communicate different aspects of the same comparison; they do not constitute separate trials or independent evidence. The registry record does not report the confidence-interval construction method, so its specific assumptions cannot be evaluated from the record.

Precision is limited by the observed data and by the endpoint definition, population, and follow-up period. The interval does not establish equivalence, and its inclusion of effects on either side does not identify which values are clinically important. A clinical importance threshold is not reported in the registry record. The non-inferiority margin is also not reported, so the interval cannot be judged against a registry-stated margin.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are expressed as participants per arm for this binary endpoint. They are not total events. The assumptions stated for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the target effect is a stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

For the primary endpoint, planning for 100% of the observed effect gives 106,420 participants per arm for 80% power and 142,466 participants per arm for 90% power. Planning for 75% of the observed effect gives 190,135 participants per arm for 80% power and 254,536 participants per arm for 90% power. Planning for 50% of the observed effect gives 429,923 participants per arm for 80% power and 575,544 participants per arm for 90% power.

In plain terms, the 80% power column describes the illustrative number of participants per arm needed, under the stated assumptions, for an 80% chance of detecting the chosen effect at the stated significance level if that effect were the true effect and the model assumptions held. The 90% column uses the corresponding higher target chance of detection. These are prospective planning illustrations, not a description of what happened in the trial.

The smaller the effect a study aims to detect, the more participants it generally needs, all else equal. That pattern appears across the listed effect fractions: the planning counts increase as the assumed effect moves from 100% to 75% to 50% of the observed effect. This is not observed power; it is a planning calculation based on the observed estimate and the stated assumptions. It should not be interpreted as a retrospective measure of whether the trial was adequately powered.

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 = 0.075; treatment proportion p₁ = 0.071; average p̄ = 0.073.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3679 = 0.7210.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3679 = 0.3096.
4. n = (0.7210 + 0.3096)² / (-0.0032)² = 106,419.9, rounded up to 106,420 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 <- 0.0745692980200566                          # control proportion
p1 <- 0.0714100905562743                          # 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(305162)
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 = 106,420 (80% power), 142,466 (90% power)
 75% of observed effect: n per arm = 190,135 (80% power), 254,536 (90% power)
 50% of observed effect: n per arm = 429,923 (80% power), 575,544 (90% power)
power.prop.test: 106419.9 
Simulated power at n = 106,420 per arm: 0.800 (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

Multiplicity arises when a study evaluates several outcomes, components, time points, or analysis populations. Even when each individual test uses a conventional threshold, repeated testing can increase the chance of a false-positive finding somewhere among the tests. The registry record lists 17 outcome measures, including 16 secondary outcomes, and the posted secondary comparisons are unadjusted. A multiplicity adjustment or prespecified hierarchy for interpreting those outcomes is not reported in the registry record.

The primary endpoint is a composite, and the registry also lists individual outcomes and other combinations. Examining several related endpoints can be scientifically informative, but it creates a need to distinguish the main confirmatory question from supporting or exploratory analyses. The registry record states a superiority or non-inferiority objective but does not report the formal testing sequence, a non-inferiority margin, or how the type I error would be controlled across the objectives. Consequently, the posted results cannot establish whether a particular formal multiplicity strategy was used.

The primary population is described as mITT, excluding STEMI. The registry record does not report a fuller definition of mITT, the handling of participants with missing endpoint status, how withdrawals were treated, or whether other analysis populations were prespecified. The endpoint denominators are stated, but counts alone do not reveal missingness patterns or whether every randomized participant contributed an outcome.

These gaps affect interpretation rather than changing the posted values. Missing-data assumptions can influence an estimate if outcome status is unavailable, and analysis-population choices can affect which participants contribute to a comparison. The registry record does not report sensitivity analyses for missing data, protocol deviations, or alternative populations. It also lists the trial status as terminated without reporting a reason. These details should not be inferred from the outcome counts or from the statistical results.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0.5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: ventricular fibrillation (0.3%), renal failure acute (0.3%), chest pain (0.2%), cardiogenic shock (0.2%), hypotension (0.2%).

The safety record reports serious adverse events affecting 125 participants at risk out of 4374 in the cangrelor group and 127 participants at risk out of 4365 in the clopidogrel group. Other adverse events affected 1149 participants at risk out of 4374 and 1159 participants at risk out of 4365, respectively. These figures describe reported counts in the safety record; they do not, by themselves, establish a comparative safety advantage.

The most frequently listed serious adverse event terms and their recorded percentages are ventricular fibrillation, 0.3%; renal failure acute, 0.3%; chest pain, 0.2%; cardiogenic shock, 0.2%; hypotension, 0.2%; and cardiac arrest, 0.1%. The registry record does not specify in this information whether these term percentages are presented by treatment arm or how the terms were selected. It also does not report the safety observation period, event relatedness, or the method for coding adverse events.

The safety at-risk counts differ from the primary endpoint denominators, and the registry record does not explain the population definitions. Death counts are not reported in the registry record. The counts should therefore be read as recorded safety summaries, not as a complete assessment of comparative risks or causality.

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

The posted primary result describes the difference observed between the cangrelor and clopidogrel arms for the composite of all-cause mortality, MI, or IDR during the interval from randomization through 48 hours after randomization in the mITT population excluding STEMI. The point estimate is small, and its confidence interval includes differences in either direction. The unadjusted p-value does not provide strong evidence against a no-difference hypothesis under the test used, but it does not prove that the treatments have identical effects.

The result does not establish superiority. Nor does a failure to demonstrate superiority establish non-inferiority. A non-inferiority conclusion requires a specified margin and a prespecified analysis suitable for that objective; the margin and formal procedure are not reported in the registry record. The interval should not be used to claim equivalence in the absence of an equivalence framework and clinically justified bounds.

The result is specific to the composite definition, the mITT population excluding STEMI, and the short follow-up window stated in the record. It does not establish what happened beyond that window, in a different patient population, or for any one component considered alone. The posted counts do not convey how outcomes were adjudicated, how missing observations were treated, or whether the analysis followed a prespecified plan.

Safety summaries add descriptive information but do not resolve the primary efficacy question or establish comparative safety. Their denominators differ from those used for the primary endpoint, and relevant safety methods are not reported in the registry record. The trial’s terminated status also warrants caution in interpreting the record, but the reason for termination is not reported and should not be presumed. In general, the most defensible reading is descriptive: the posted data show a close observed primary comparison with uncertainty that remains compatible with effects in either direction.

17. Why This Trial Matters Statistically

This trial illustrates why a clinical objective and an observed comparison are not interchangeable. The registry states a goal of showing superiority or at least non-inferiority, while the posted primary estimate is a near-zero risk difference with an interval crossing the no-difference point. Interpreting whether either objective was met requires more than the point estimate: a non-inferiority margin, prespecified test, and analysis plan are essential, and those details are not reported in the registry record.

The composite endpoint also demonstrates a common statistical trade-off. Combining mortality, MI, and IDR produces a single summary for whether a participant experienced a listed event, but it can conceal variation among components. Separate component outcomes can add context, yet testing many related outcomes without a reported multiplicity strategy makes isolated secondary findings less secure.

The record further shows the importance of matching each statistic to its population and purpose. The primary endpoint uses an mITT population excluding STEMI, while safety summaries have different at-risk counts. The sample-size illustrations are prospective planning exercises based on the observed effect and stated assumptions; they are not observed power and do not reveal the original design rationale.

More broadly, registry results are most useful when estimates, uncertainty, endpoint definitions, populations, and analysis plans can be considered together. The posted data allow readers to describe the primary comparison and its imprecision, but absent analysis details constrain stronger claims. Distinguishing what the result estimates from what it cannot establish is central to sound interpretation of clinical trial statistics.

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.

Several trial-specific limitations are evident in the registry record. The trial is listed as terminated, but a reason for termination is not reported. The registry states that the objective was superiority or at least non-inferiority, yet the non-inferiority margin and formal testing strategy are not reported. Without those details, the posted result cannot be used to determine whether a non-inferiority criterion was met.

The primary endpoint is a composite observed through 48 hours after randomization. The record does not provide component-specific primary analysis details beyond the listed secondary outcome summaries, nor does it report the adjudication process or how multiple components were counted. The short stated timeframe also limits conclusions to early events and does not establish longer-term outcomes.

The analysis population is identified as mITT excluding STEMI, but the registry record does not give a complete population definition or explain how missing outcome data and protocol deviations were handled. The safety denominators differ from the primary endpoint denominators, with no explanation of the population difference. Such distinctions matter when comparing efficacy and safety summaries.

The record lists multiple secondary outcomes and posts unadjusted comparisons, but does not report a multiplicity plan or a complete statistical analysis plan. It does not report interim analyses, original sample-size justification, or the original trial design assumptions. The posted sample-size planning figures are based on the observed effect and a stated illustration model, rather than the trial’s own design. These limitations do not invalidate the reported counts, but they restrict how strongly the estimates can support confirmatory claims.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Clinical Trial to Demonstrate the Efficacy of Cangrelor — NCT00305162.
• Registry record last updated 2014-05-08; status last verified 2014-04.
• Results first posted 2014-04-23.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a randomized, triple-masked, parallel-group phase 3 trial comparing cangrelor with clopidogrel in subjects requiring PCI. Enrollment is listed as 8882, and the study status is terminated. The primary endpoint is a composite of all-cause mortality, MI, and IDR from randomization through 48 hours after randomization in an mITT population excluding STEMI.

The posted primary risk difference is -0.003, with a 95% confidence interval from -0.015 to 0.008 and an unadjusted p-value of 0.593. The interval is compatible with differences in either direction and does not establish superiority, equivalence, or non-inferiority. The non-inferiority margin, detailed analysis plan, missing-data methods, multiplicity strategy, and reason for termination are not reported in the registry record.