Pharmacodynamic Evaluation of Switching From Prasugrel to Ticagrelor: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pharmacodynamic Evaluation of Switching From Prasugrel to Ticagrelor (NCT02016170), a randomized na study. The primary outcome is Platelet Reactivity Measured as P2Y12 Reaction Units (PRU) Determined by Verify Now-P2Y12 Assay.

2. Clinical Question

The question is pharmacodynamic: it concerns platelet reactivity, not recurrent ischemic events or other clinical outcomes. PRU is the primary measure, obtained with the Verify Now-P2Y12 assay. Lower posted mean PRU values indicate lower measured platelet reactivity; the analysis does not by itself establish what a particular value means for an individual patient's clinical outcome.

The study also assessed Platelet Reactivity Index (PRI), measured by whole blood vasodilator-stimulated phosphoprotein. That secondary measure gives a related, but distinct, laboratory view of platelet reactivity. Agreement in the direction of results across measures can inform interpretation, while neither measure substitutes for evidence about clinical events.

The registry record describes a prospective, randomized, parallel pharmacodynamic investigation and says its aim was to show similar levels of platelet inhibition after switching. It does not report the decision threshold that would define non-inferiority. Therefore, the posted estimates can be interpreted as comparisons of measured values, but the record does not support a definitive judgment against a prespecified non-inferiority criterion.

3. Trial Design

SWAP-3 is recorded as a completed, randomized, parallel-design study sponsored by the University of Florida. The registry record lists enrollment of 82 and identifies coronary artery disease and acute coronary syndrome as the conditions. The study was not masked. Its phase is listed as NA.

The intervention descriptions distinguish ticagrelor 180mg as a loading dose and ticagrelor 90mg as a maintenance dose for patients switching from prasugrel. The third regimen was continuation of prasugrel 10mg. In the primary endpoint description, the two switched-to-ticagrelor arms are combined and compared with the prasugrel group. The posted primary outcome results likewise present a combined Ticagrelor group and a Prasugrel group, whereas safety results are separated by the three named regimens.

The primary assessment was at 7 days. The registry describes the analysis population as patients who received randomized treatment and had a valid primary endpoint value, defined as PRU at 1 week. It does not give further detail about the randomization sequence, concealment, stratification, or handling of participants who did not meet that analysis-population definition. These aspects are not reported in the registry record.

Enrollment and analysis-population counts should not be treated as interchangeable. Enrollment is recorded as 82, while the primary endpoint groups report 52 in the Ticagrelor group and 27 in the Prasugrel group. The record does not explain the full flow from enrollment through treatment and endpoint availability, so reasons for any difference are not reported in the registry record.

The stated study objective was to examine whether switching provided similar platelet inhibition. The registry record does not report the original sample-size justification, the non-inferiority margin, or details of the planned statistical analysis. Those omissions limit assessment of whether the design had a prespecified basis for its intended non-inferiority claim.

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: One patient was excluded after providing informed consent because of inadequate venous access. Thus a total of 82 patients were randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Analysis was conducted in patients who received the randomized treatment and had a valid primary end point value (PRU at 1 week).

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 Platelet Reactivity Measured as P2Y12 Reaction Units (PRU) Determined by Verify Now-P2Y12 Assay, measured over 7 days.

The primary endpoint is platelet reactivity measured as P2Y12 Reaction Units (PRU) with the Verify Now-P2Y12 assay. PRU is a continuous laboratory measurement: it can take a range of values rather than placing participants only into categories. The registry reports least-squares means and standard errors for this endpoint at 7 days.

Platelet reactivity is used in a pharmacodynamic study because it measures a biological response to antiplatelet treatment. In this study, the specific question was whether the measured PRU level after switching from prasugrel to ticagrelor was non-inferior to the level among patients who continued prasugrel. This is a comparison of laboratory response, not a direct test of whether the treatments differ in clinical events.

The primary hypothesis combines the ticagrelor switching arms. That pooled comparison addresses the registry's stated question about switching overall, but does not separately establish the effect of each ticagrelor regimen. The separate dosing descriptions remain important context, particularly because the safety results are listed by regimen.

For a continuous endpoint, a group mean conveys the average measurement, while a standard error describes uncertainty in estimating that mean. A comparison of means estimates the average difference between groups. To assess non-inferiority, however, the estimated difference must be judged against a prespecified margin. The margin is not reported in the registry record, so the posted PRU comparison alone cannot confirm that the study met a non-inferiority criterion.

7. Results Posted in the Registry

• Prasugrel: mean 63.00 versus 45.00 on control; difference 18.00 (95% CI -3.20 to 39.20), standardized effect d = 0.40; z-test p = 0.096.

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.

Platelet Reactivity Index (PRI) Measured by Whole Blood Vasodilator-stimulated Phosphoprotein (VASP).

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Prasugrel: mean 36.00 versus 25.00 on control; difference 11.00 (95% CI 7.23 to 14.77), standardized effect d = 1.54; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Prasugrel than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary PRI measure follows the same broad direction as the primary PRU result: the posted group averages indicate lower platelet reactivity in the Ticagrelor group than in the Prasugrel group. The secondary comparison is more clearly separated statistically than the primary comparison, but it remains a secondary pharmacodynamic finding. It does not independently establish the primary non-inferiority hypothesis or translate directly into a clinical outcome.

PRI and PRU are related laboratory measures, but they are not identical endpoints. Seeing a similar direction across them offers a form of internal consistency for the measured platelet response. It does not eliminate uncertainty about the primary analysis, compensate for the unreported non-inferiority margin, or show that the difference changes the risk of clinical events.

Unadjusted secondary findings carry less weight when several outcomes or comparisons may be examined. In general, testing multiple outcomes increases the chance that at least one result will appear statistically notable by chance alone. Procedures such as multiplicity adjustment or a prespecified hierarchy can address that issue, but the registry record does not report such a strategy. The degree to which the secondary finding was planned or protected against multiplicity is therefore not reported in the registry record.

The registry lists one secondary outcome, while the record also reports outcome and analysis counts without explaining the full analysis structure. The posted secondary result is useful as supporting context, but should not be treated as an independent confirmation of a clinical benefit or as a reason to disregard the more qualified interpretation of the primary result. The overall evidence remains focused on platelet reactivity at 7 days in the recorded analysis population.

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

• Platelet Reactivity Index (PRI) Measured by Whole Blood Vasodilator-stimulated Phosphoprotein (VASP).

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish what the posted results estimate from what they can establish. These explanations are general statistical concepts; the registry record does not report every detail of the methods used in the sponsor's analysis.

What does a group mean describe?

A mean is an average of the measurements in a group. For a continuous measure such as PRU or PRI, it summarizes the group's central level, but does not show the full distribution of individual measurements. Two groups can have different means while their individual values overlap substantially. A group mean therefore should not be interpreted as a value that every participant experienced.

The primary outcome is labelled as a least-squares mean. In general, a least-squares mean is a model-based estimate rather than necessarily the raw arithmetic average. The registry record does not report the model or adjustments used to obtain the sponsor's least-squares means, so the details of that estimation cannot be assessed from the record. The re-calculation described separately is based on posted summary statistics and is not an adjusted model analysis.

What does a standard error describe?

A standard error describes the sampling uncertainty in an estimated quantity, such as a group mean. It is not the spread of individual participant values. A standard deviation, in contrast, describes variation among observed measurements. The primary endpoint reports standard errors; the secondary endpoint is labelled with standard deviations. Those dispersion measures are not interchangeable, so they should be read according to the definition used for each outcome.

In general, a smaller standard error indicates a more precise estimate under the assumptions of the analysis. It does not remove potential bias from missing observations, limitations in the analysis model, or other design issues. Nor does a precise estimate alone answer whether a difference is clinically important or meets a non-inferiority criterion.

How should a mean difference be read?

A mean difference is the estimated difference between group means. Its sign depends on which group is subtracted from which. The registry's reported primary difference is -18, while the simple re-calculation expresses the same comparison in reverse order as 18.0. The sign change reflects the order of subtraction, not a different set of observed group means. Always read a difference alongside its group order and the confidence interval.

A confidence interval gives a range of values compatible with the estimate under the statistical model and its assumptions. If an interval for a difference includes zero, the data do not rule out no difference at the confidence level used. That is not proof that the groups are equal. For a non-inferiority question, the relevant comparison is with the prespecified margin, not merely with zero.

Why does non-inferiority require a margin?

Non-inferiority asks whether a treatment is not worse than a comparator by more than an acceptable amount. That acceptable amount is defined by a margin set before examining the results. The margin determines the boundary against which the estimate and its uncertainty are judged. Without the margin, a reader cannot determine whether the confidence interval is sufficiently favorable for a non-inferiority conclusion. The registry record describes the hypothesis but does not report the margin, so the necessary decision rule is unavailable.

Equivalence is a related but distinct question: it generally requires the plausible difference to lie within bounds in both directions. A registry label that refers to non-inferiority or equivalence does not, on its own, supply the analysis definition or establish that either criterion was satisfied. The posted primary result is best read as an estimated group difference with uncertainty unless the missing decision details are available elsewhere in the registry record.

Why can over-dispersion matter?

In general, a statistical model may assume a particular amount of variability in its outcome. Over-dispersion occurs when actual variability is greater than the model allows. If that extra variability is ignored, standard errors can be too small and confidence intervals too narrow, making results appear more precise than warranted. This is a general consideration for statistical modeling, not a claim that over-dispersion occurred in this study. The registry record does not report enough detail to assess that issue for the sponsor's analysis.

What is the role of the re-calculation?

The unadjusted re-calculation uses posted group summary statistics to estimate a difference and its uncertainty. Such a calculation can help readers check the broad relationship between the group estimates and compare that with the sponsor's reported result. It may differ from a sponsor analysis because the sponsor may have used a model, adjustment, or variance estimate not recoverable from the summary statistics. The sponsor's reported analysis remains the primary account of the study's own result; the re-calculation should not be treated as a substitute or as a definitive reconstruction of the original analysis.

The registry record does not report a detailed statistical analysis method, an adjustment set, or whether analyses were prespecified beyond the stated primary hypothesis. It also does not report a multiplicity strategy. These gaps matter because analytic choices can affect estimates, uncertainty, and how much confidence should be placed in secondary findings.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a quantity, and the confidence interval communicates uncertainty around a group difference. The sponsor's primary estimate is -18, with a 95% confidence interval from -41 to 5. The interval spans zero and includes values on both sides of no difference. This means the posted result is compatible with a range of possible group differences; it does not show that the groups are identical.

The primary confidence interval is broad enough to include both a difference favoring Ticagrelor under the sponsor's subtraction order and a difference in the other direction. The record does not report a non-inferiority margin, so the interval cannot be compared with the threshold needed to assess the stated non-inferiority hypothesis. Whether it is sufficiently precise for that purpose is therefore not reported in the registry record.

The unadjusted re-calculation gives a 95% confidence interval from -3.2 to 39.2 for the difference expressed in the reverse order. Although its endpoints have a different sign orientation, the interval also includes zero. This re-calculated interval is derived from summary statistics and should not be mistaken for the sponsor's analysis or for a formal non-inferiority interval.

Confidence intervals express uncertainty under the assumptions of the method used; they do not account for every possible source of error. They do not address unreported missing-data mechanisms, uncertainty about the analysis plan, or whether the study's enrolled population represents other populations. The reported precision is also specific to this endpoint and analysis population, not a measure of precision for clinical events or safety outcomes.

For the secondary PRI outcome, the posted comparison is more clearly separated from zero than the primary PRU comparison. That statistical pattern should still be considered in light of its secondary status, the lack of a reported multiplicity approach, and the fact that the registry does not report a comprehensive analysis plan. Confidence intervals can describe uncertainty for each estimate, but do not by themselves correct for examining multiple outcomes.

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 for the continuous-outcome comparison. They are not total event counts. The underlying illustration assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It uses the observed effect as a reference and considers planning for 100% of that effect, 75% of the observed effect, and 50% of the observed effect.

The 80% power column gives the participants per arm that the illustration estimates would be needed for an 80% chance of detecting the stated effect under those assumptions. The 90% power column gives the corresponding participants per arm for a 90% chance. Power is a design calculation: it describes the probability of detecting an effect of the specified size if that effect is real and the assumptions hold. These are planning illustrations based on the observed effect, not the trial's original sample-size justification; that justification is not reported in the registry record.

The rows show why the assumed effect size matters. Planning for 75% of the observed effect requires more participants per arm than planning for 100% of the observed effect, and planning for 50% requires more still. Smaller effects are harder to distinguish from random variation, so they generally require more participants to reach the same power target. The higher power target also calls for more participants per arm than the lower target for a given assumed effect.

These figures are not observed power. They should not be used to claim that the completed trial had a particular probability of success after its results were known. They are hypothetical planning references under stated assumptions, and may not reflect the original design, its non-inferiority objective, or any unreported features of the actual analysis.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 18.000; pooled standard deviation σ = 44.479.
2. n = 2 × (1.96 + 0.842)² × 44.479² / 18.000² = 95.9, rounded up to 96 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
delta <- 18                      # observed difference in means
sigma <- 44.4787998530045                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2016170)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 96 (80% power), 129 (90% power)
 75% of observed effect: n per arm = 171 (80% power), 229 (90% power)
 50% of observed effect: n per arm = 384 (80% power), 514 (90% power)
power.t.test: 96.8 
Simulated power at n = 96 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor's primary analysis as a mean difference of -18, with a 95% confidence interval from -41 to 5. A p-value and analysis method are not reported for this result. The estimate is presented in the sponsor's group order and should be read as the study's own reported analysis.

The simple re-calculation from the posted group summaries expresses the comparison in reverse order: it gives a mean difference of 18.0, a 95% confidence interval from -3.2 to 39.2, and p = 0.096. The opposite sign reflects the reversed subtraction order. The calculation is unadjusted and may not reproduce the sponsor's method, which is not described in detail in the registry record.

The record does not flag a discrepancy between its reported analysis and the re-calculation. Even so, the sponsor's own result takes priority when describing what the study reported; the re-calculation is supplementary and should not be presented as the sponsor's analysis. Both intervals include zero, but that does not resolve the non-inferiority question. The margin required to interpret the primary hypothesis is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators test multiple outcomes, comparisons, time points, or analysis choices. Even if each individual test uses a conventional significance threshold, examining many tests can increase the chance of at least one apparently notable result arising by chance. Statistical plans may manage this through adjustment, a hierarchy of outcomes, or clear designation of which analyses are confirmatory and which are exploratory.

The registry identifies PRU as the primary outcome and PRI as a secondary outcome. It reports two outcome measures and two analyses, but does not describe a multiplicity adjustment or testing hierarchy. Whether the analyses were adjusted, or how the primary and secondary claims were prioritized, is not reported in the registry record. The secondary finding should therefore be interpreted as supportive context rather than as an independent confirmatory result.

The primary endpoint population is defined as patients who received randomized treatment and had a valid PRU value at 1 week. This is an available-endpoint analysis population, but the record does not report how many enrolled participants lacked a valid endpoint, why values were missing, or whether missingness was related to treatment or outcome. The methods for handling missing data, if any, are not reported in the registry record.

The record also does not describe whether an intention-to-treat analysis, a per-protocol analysis, or sensitivity analyses were conducted. This is particularly relevant to a non-inferiority question, for which different analysis populations can be informative. No assumptions about those analyses should be inferred from the stated endpoint population alone.

Finally, the non-inferiority margin and the detailed statistical plan are not reported. The registry record does not report interim analyses, the original sample-size justification, or methods for adjustment of the primary estimate. These omissions do not invalidate the posted data, but they limit independent assessment of the analysis decisions and of the strength of the intended non-inferiority conclusion.

16. 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% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: angioedema (3.7%).

Safety results are reported separately for Ticagrelor 180mg, Ticagrelor 90mg, and Prasugrel 10mg. The serious adverse event counts are 1 among 27 at risk for Ticagrelor 180mg, 0 among 28 at risk for Ticagrelor 90mg, and 0 among 27 at risk for Prasugrel 10mg. The registry also lists Angioedema at 3.7% among the top serious adverse event terms.

These are descriptive counts from the reported safety groups. The small group sizes and limited number of serious events mean the counts provide little precision for comparing uncommon harms. They do not establish that a group has no risk because no serious event was recorded in it, and they do not establish a causal treatment effect.

Other adverse event counts are also listed by regimen: 10 among 27 at risk for Ticagrelor 180mg, 7 among 28 at risk for Ticagrelor 90mg, and 0 among 27 at risk for Prasugrel 10mg. These figures are not a substitute for a complete description of event definitions, severity, timing, or participant-level overlap, which is not reported in the registry record. Deaths are not reported in the record.

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

The results describe platelet reactivity measured after 7 days among patients in the recorded primary analysis population. The group means are lower for Ticagrelor than for Prasugrel on the primary PRU measure, and the secondary PRI result follows the same broad direction. The primary sponsor estimate has a 95% confidence interval that includes zero, so the posted data do not clearly distinguish the group means under that analysis.

This does not mean the treatments are proven equal. A non-significant comparison is not evidence of equivalence, and the primary objective was non-inferiority rather than ordinary superiority testing. A non-inferiority conclusion requires a margin chosen in advance and a comparison of the confidence interval with that margin. Since the margin is not reported in the registry record, the primary hypothesis cannot be evaluated fully from the posted information.

The study concerns a laboratory measure of platelet response. It does not report evidence about recurrent ischemic events, survival, or other clinical outcomes as study endpoints in the results. A change in PRU or PRI cannot on its own be converted into a claim about clinical benefit or harm.

The safety counts are descriptive and arise from groups with limited numbers of participants and few serious events. They do not provide precise comparative estimates of uncommon adverse events. Neither absence of a recorded serious event in a group nor the listed adverse event counts establish that a regimen is risk-free or that one regimen is safer.

Overall, the registry record supports a cautious account of pharmacodynamic measurements and their uncertainty. It does not support advice about treatment choice, a claim that switching improves outcomes, or a definitive conclusion that switching is non-inferior. Those conclusions would require information and evidence beyond the endpoint summaries reported in this record.

18. Why This Trial Matters Statistically

This trial is statistically interesting because its central question is non-inferiority, a design objective that cannot be judged by asking only whether a conventional test finds a difference. The estimate, its uncertainty, and the prespecified margin must be considered together. Here, the registry record describes the non-inferiority hypothesis but does not report the margin. That omission illustrates why a stated objective is not enough to establish that its statistical criterion was met.

The study also demonstrates the distinction between an endpoint's biological relevance and its clinical interpretation. PRU and PRI measure platelet reactivity, making them suitable pharmacodynamic outcomes for examining the response to a treatment switch. However, a laboratory difference does not automatically establish a difference in clinical events. Keeping that distinction clear prevents a mechanistic result from being overstated.

Another useful feature is the comparison of the sponsor's reported result with a simple re-calculation from summary statistics. The signs differ because the group order is reversed, while the broad uncertainty remains. This illustrates why group order and analysis method matter when reading mean differences, and why an unadjusted reconstruction should not replace the study's reported analysis.

Finally, the separate presentation of dosing regimens for safety and combined ticagrelor groups for the primary endpoint highlights that analysis populations can differ by question. Understanding which groups are combined, which are separate, and which participants contribute to each endpoint is essential to interpreting clinical trial summaries without assuming that every result uses the same grouping or population.

19. Limitations

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

The most consequential limitation for interpreting the primary objective is that the non-inferiority margin is not reported in the registry record. Without it, the primary confidence interval cannot be judged against the study's intended decision boundary. The detailed statistical method is also not reported, including any model or adjustment underlying the sponsor's least-squares means.

The primary endpoint analysis includes patients who received randomized treatment and had a valid PRU value at 1 week. The record does not explain the participant flow into this population or describe missing-data methods. It is therefore not possible to assess from the registry record whether missing endpoint values could have influenced the group comparison.

The primary endpoint combines the ticagrelor switching arms, while safety results are given separately by regimen. This supports an overall comparison for the stated primary question but does not provide a separate primary efficacy estimate for each dosing regimen. The record does not report a detailed rationale for this grouping.

The study is a pharmacodynamic investigation with a 7-day endpoint. The posted results concern platelet reactivity rather than longer-term clinical outcomes. The safety counts are also limited in precision for uncommon events, and deaths are not reported in the registry record. The registry does not report a multiplicity strategy, interim analysis details, or the original sample-size justification. These omissions limit evaluation of confirmatory status, precision planning, and the robustness of the reported conclusions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Pharmacodynamic Evaluation of Switching From Prasugrel to Ticagrelor — NCT02016170.
• Registry record last updated 2024-07-03; status last verified 2024-06.
• Results first posted 2016-10-18.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes SWAP-3 as a completed, randomized, unmasked, parallel pharmacodynamic study with enrollment of 82. It compared a combined group switched from prasugrel to ticagrelor with a group continuing prasugrel, assessing primary PRU at 7 days. PRI was also reported as a secondary laboratory outcome.

The primary sponsor estimate is a mean difference of -18, with a 95% confidence interval from -41 to 5. The interval includes zero, and the non-inferiority margin needed to evaluate the stated primary hypothesis is not reported. The secondary result follows the same general direction, but its interpretation is limited by its secondary status and the unreported multiplicity approach.

The record provides descriptive safety counts by regimen. It does not report detailed methods for missing data, the original sample-size justification, or the full statistical analysis plan. The findings should be read as estimates of short-term platelet reactivity, not as evidence of clinical benefit, equivalence, or comparative safety.