Investigation of the Athero-Protective Effects of Clopidogrel: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Investigation of the Athero-Protective Effects of Clopidogrel (NCT01283282), a randomized phase 4 study. The primary outcome is Flow-mediated Dilation (FMD).

2. Clinical Question

3. Trial Design

The registry describes a completed Phase 4, randomized, quadruple-masked crossover study sponsored by Emory University. The study start is recorded as 2008-01 and primary completion as 2010-12. Its condition is coronary artery disease, and enrollment is listed as 48.

Participants were assigned to one of two treatment sequences. One sequence began with clopidogrel 75 mg daily for 6 weeks and then changed to placebo daily for 6 weeks. The other began with placebo daily for 6 weeks and then changed to clopidogrel for 6 weeks. The registry summary describes a 12 week study and says participants continued their prescribed medical therapy. In a crossover design, each participant is intended to receive both treatments, so within-participant comparisons can be important. The registry record does not describe how treatment-period effects or within-participant correlation were handled in the reported analysis.

Quadruple masking indicates that masking was recorded at four roles in the registry design classification; the record does not identify the roles in this entry. The summary states that neither participants nor researchers would know which treatment was being taken. The listed interventions are clopidogrel and placebo.

The primary endpoint is FMD, with a stated unit of percent change in diameter and a timeframe of baseline and Week 12. Secondary outcomes include pulse wave velocity, oxidative stress markers, high-sensitivity C-reactive protein, and CD40 ligand. Although the registry lists enrollment as 48, the posted endpoint summaries report n=41 for each treatment group. The registry record does not explain the relationship between the enrollment count and the numbers in the endpoint summaries, or whether any participants lacked outcome data.

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.

First Intervention (6 Weeks)

Reasons for not completing this period:

Second Intervention (6 Weeks)

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: 41 subjects completed the entire study.

6. Primary Endpoint

The registry lists the primary outcome as Flow-mediated Dilation (FMD), measured over Baseline, Week 12.

Flow-mediated dilation (FMD) measures the change in brachial artery diameter in response to a blood-flow stimulus. In this study it was collected by ultrasound and expressed as percent change in diameter. The registry describes the endpoint as a measure from baseline to 12 weeks, and lists its timeframe as baseline and Week 12.

FMD is used as a physiological measure of vascular function. As a continuous endpoint, it can capture differences across a range rather than sorting observations into only event/no-event categories. Its interpretation depends on how it was measured, the timing of assessment, the variability of the measure, and the treatment comparison used. The registry record does not report further procedural details about the ultrasound assessment, such as reproducibility or assessor procedures.

The posted mean FMD values are 4.89 for clopidogrel and 4.81 for placebo. The unadjusted mean difference is 0.08, with a confidence interval from -1.555 to 1.715. The interval spans values in either direction, so the posted estimate is not precise enough to determine a clear treatment contrast. A near-zero point estimate by itself does not show that the treatments are equivalent, and the registry record does not report an equivalence margin or a formal equivalence analysis.

7. Results Posted in the Registry

• Clopridogrel: mean 4.89 versus 4.81 on control; difference 0.08 (95% CI -1.56 to 1.72), standardized effect d = 0.02; z-test p = 0.924.

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.

Pulse Wave Velocity (PWV)

• 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 errors.
• Result:
  • Clopridogrel: mean 8.77 versus 9.04 on control; difference -0.27 (95% CI -1.52 to 0.97), standardized effect d = -0.10; z-test p = 0.667.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Clopridogrel and the control. The interval gives the range of effects that remain compatible with the data.

Inflammatory Marker High-sensitivity C-reactive Protein (hsCRP)

• 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 errors.
• Result:
  • Clopridogrel: mean 5.98 versus 4.31 on control; difference 1.67 (95% CI -3.74 to 7.08), standardized effect d = 0.13; z-test p = 0.545.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Clopridogrel and the control. The interval gives the range of effects that remain compatible with the data.

Inflammatory Marker CD40 Ligand

• 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 errors.
• Result:
  • Clopridogrel: mean 1,202 versus 2,169 on control; difference -967.11 (95% CI -1,850 to -84.71), standardized effect d = -0.47; z-test p = 0.032.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Clopridogrel than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several related but distinct domains: arterial stiffness, oxidative stress, and inflammatory markers. The posted results therefore broaden the description beyond FMD, but they do not all measure the same biological or physiological feature. Their results should not be expected to form a single interchangeable measure of vascular function.

Across the reported secondary comparisons, the pattern is not uniform. Estimates differ in direction and precision, and only one of the posted unadjusted confidence intervals excludes zero. This does not provide a consistent set of secondary findings that independently confirms the primary comparison. Nor does a mixed pattern prove that there are no effects across these outcomes; the estimates remain subject to uncertainty and to the limitations of the reported analysis.

The secondary findings are most useful as context for the primary result and as information about measures the trial chose to observe. They do not replace the primary endpoint, and they should not be treated as though each were a separate confirmatory trial. Several outcomes are listed, but the registry record does not report a plan for controlling the chance of false-positive results across them. Without such a plan, unadjusted p-values carry less weight, particularly when one result stands apart from the broader pattern.

The registry lists oxidative stress markers among secondary outcomes, but the posted secondary results described in the record include pulse wave velocity, hsCRP, and CD40 ligand. The registry record does not report a corresponding posted numerical outcome for oxidative stress markers. It also does not report formal analyses for the secondary outcomes. Taken together, the secondary results are exploratory evidence about the measured endpoints, not a definitive resolution of the primary question.

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

• Pulse Wave Velocity (PWV)
• Oxidative Stress Markers
• Inflammatory Marker High-sensitivity C-reactive Protein (hsCRP)
• Inflammatory Marker CD40 Ligand

9. Statistical Interpretation

10. Statistical Methods Explained

The results concern continuous outcomes, summarized as means with standard errors. A mean describes the central value of a set of measurements. A standard error describes the uncertainty in an estimated mean; it is not the same as the spread of individual participants’ values. The registry identifies standard error as the reported dispersion for the primary and secondary outcomes.

What does a mean difference represent?

A mean difference compares the reported mean under clopidogrel with the reported mean under placebo. The sign indicates the direction of that contrast under the stated ordering: a positive difference means the clopidogrel mean is higher, and a negative difference means it is lower. The primary mean difference is 0.08. The secondary mean differences are reported in their own measurement units. These are unadjusted contrasts, not estimates adjusted for participant characteristics or other covariates.

The comparison values are simple unadjusted recalculations from the posted summary statistics. They are not a substitute for a complete analysis of the crossover trial. The registry record does not report a statistical model, an analysis population, or details of how participant-level measurements were incorporated. Since each participant was assigned to receive both treatments in a sequence, a paired analysis may be relevant, but the record does not say whether one was used. It also does not report how period or sequence effects were addressed.

How should the confidence interval be read?

A confidence interval gives a range of values compatible with the estimate under the method used, reflecting sampling uncertainty. A narrower interval indicates greater precision; a wider interval indicates less precision. If an interval for a mean difference includes zero, the data are compatible with no mean difference under that analysis, as well as with differences on either side of zero. This does not prove that the true difference is zero. The primary interval extends from -1.555 to 1.715, so it includes zero and permits a range of possible contrasts.

Confidence intervals describe uncertainty in an estimate; they do not show the distribution of individual outcomes and do not indicate the probability that a particular treatment is better. Their interpretation also depends on the method used to construct them. The registry record does not report the interval-construction method or whether the reported comparisons account for the crossover structure.

What does a p-value add?

A p-value describes how incompatible the observed data are with a specified null hypothesis under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, and it does not quantify the size or importance of an effect. The primary unadjusted p-value is 0.924. The registry record does not report the test or model behind the sponsor’s analysis, and its outcome-analysis listing contains no reported analyses. The posted p-values should therefore be read as unadjusted statistical summaries, not as a full account of the planned analysis.

Unadjusted p-values do not account for testing multiple endpoints. When many outcomes are examined, the chance of at least one apparently unusual result can increase. This is one reason a single nominal secondary p-value warrants less weight when the record does not describe a multiplicity strategy.

Why can over-dispersion matter?

For continuous measures, the standard error reflects uncertainty in the mean and depends on the variability of measurements and the amount of information available. When observations vary more than an analysis assumes, uncertainty can be understated; this is one general form of over-dispersion. In a crossover study, within-participant dependence also matters: measurements from the same person are generally not independent in the way measurements from unrelated people might be. A method that ignores relevant dependence can misstate precision. The registry record does not report enough analytic detail to assess these issues for the posted comparisons.

The displayed standardized effect sizes and planning illustrations are derived from posted summaries and are not trial findings independent of the means and uncertainty. The planning illustrations use a normal approximation and equal allocation, with the listed significance level and target power. They are hypothetical design calculations based on fractions of the observed effect, not evidence about the study’s original design or its analysis. The original sample-size assumptions, any interim analyses, and the sponsor’s full statistical plan are not reported in the registry record.

11. Confidence Intervals and Precision

Precision is best judged by considering the estimate together with its confidence interval, rather than focusing only on the point estimate or p-value. For FMD, the mean difference is 0.08, and the 95% confidence interval ranges from -1.555 to 1.715. Because this interval includes zero and extends in both directions, the estimate does not pin down a clear direction or a narrow range of plausible contrasts.

The confidence interval is also relevant to claims of no difference. An interval that crosses zero does not show that any possible difference is negligible. Whether the range includes only unimportant differences depends on a threshold for importance, and the registry record does not report one. The record also does not report a formal equivalence analysis.

The standard error for each primary group mean is 0.59. Standard errors express uncertainty in estimated means, not the range of measurements among participants. A confidence interval for a treatment contrast depends on the comparison method and, in this crossover design, potentially on the within-participant relationship between measurements. The registry record does not describe whether the posted interval accounts for that relationship. Therefore, the interval is informative as a posted summary, but its method cannot be independently assessed from the registry entry alone.

Each treatment group’s posted endpoint summary has n=41. These outcome counts differ from the registry’s enrollment entry of 48, and the record does not explain missingness or the analysis population. Without those details, it is not possible to assess whether the reported precision could be affected by exclusions or incomplete outcome data. The interval should be understood as uncertainty around the posted comparison, not as a guarantee about the range of effects in other populations or settings.

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 80% power and participants per arm for 90% power. They are not total event counts: the outcomes in this study are continuous. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The trial’s own original design assumptions are not reported in the registry record.

The 80% power column describes a planning target under which a study would have an 80% chance of detecting the assumed effect at the specified significance level, if the calculation’s assumptions hold. The 90% column uses a higher target chance of detecting that assumed effect, and therefore generally calls for more participants. For example, the primary-endpoint illustration gives 35,007 participants per arm for 80% power and 46,864 participants per arm for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the corresponding figures are 62,234 and 83,313 participants per arm; for 50%, they are 140,025 and 187,454 participants per arm.

These figures are illustrative rather than recommendations for a future study. They rely on the observed effect, which is uncertain, and the estimated variability in the posted data. A smaller effect is harder to distinguish from random variation, so planning for a smaller effect requires more participants under the stated assumptions. These figures are not observed power: they do not measure the probability that the completed study found a real effect, and they do not explain the trial’s original design.

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 = 0.080; pooled standard deviation σ = 3.778.
2. n = 2 × (1.96 + 0.842)² × 3.778² / 0.080² = 35,006.2, rounded up to 35,007 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 <- 0.0800000000000001                      # observed difference in means
sigma <- 3.77784330008538                     # 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(1283282)
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 = 35,007 (80% power), 46,864 (90% power)
 75% of observed effect: n per arm = 62,234 (80% power), 83,313 (90% power)
 50% of observed effect: n per arm = 140,025 (80% power), 187,454 (90% power)
power.t.test: 35007.2 
Simulated power at n = 35,007 per arm: 0.800 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and multiple secondary outcomes, but it does not report how the analysis handled multiple comparisons. Testing several outcomes increases the opportunity for at least one result to appear statistically unusual by chance. Adjustments or a prespecified hierarchy can help define how findings should be interpreted across a family of tests. Neither such a strategy nor a hierarchy among the secondary outcomes is reported in the registry record.

The secondary p-values are unadjusted. They should not be interpreted as though each were the sole planned test. In particular, a nominal result among several endpoints has less evidential weight when the analysis plan and multiplicity handling are not available. The record also does not report whether the secondary outcomes were prespecified in the same form as the posted results.

Missing-data handling is not reported in the registry record. Enrollment is listed as 48, while the primary and secondary treatment-group summaries list n=41 for each group. The record does not explain why these counts differ, whether all participants completed both treatment periods, how missing measurements were treated, or whether any imputation was used. It also does not state whether the analyses included all randomized participants, only participants with complete outcomes, or another analysis population.

Those details are especially relevant in a crossover study because a participant may have measurements under one treatment, both treatments, or neither treatment. The record does not say how incomplete sequences were handled. It also does not report whether the study assessed carryover, period effects, or sequence effects, or how any such effects were addressed. These omissions limit assessment of the assumptions behind the treatment comparison.

The registry record contains no reported outcome analyses in its analysis listing. It does not provide an interim-analysis plan, a detailed statistical plan, or sample-size assumptions for the original design. These items are not evidence that the procedures were absent; they are simply not reported in the registry record.

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 5% reporting threshold.

The registry reports serious adverse events for the clopidogrel and placebo groups separately. For each group, 48 participants are listed as at risk for serious adverse events and 0 as affected. For other adverse events, each group likewise lists 48 at risk and 0 affected. These are the counts recorded in the registry entry, not a comparison adjusted for the crossover design.

The deaths field is null for both groups. A null value is not the same as a reported count of zero; deaths are not reported in the registry record. The serious-event terms list is empty, so no specific serious adverse event terms are listed.

These safety figures are limited to what the registry reports. They do not describe event timing, exposure during each treatment period, definitions, ascertainment procedures, or whether participants contributed information under both treatments. The at-risk counts in the safety entry also differ from the n=41 treatment-group counts reported for the outcome summaries; the registry record does not explain that difference. Absence of recorded affected participants in these fields should not be generalized beyond the study entry or treated as a complete safety assessment.

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

The posted primary comparison describes a mean FMD difference of 0.08, with a 95% confidence interval from -1.555 to 1.715 and an unadjusted p-value of 0.924. The estimate is close to zero, but its interval includes both negative and positive contrasts. The result therefore does not provide a precise estimate of the direction or size of a treatment difference in this study.

It does not establish equivalence, because the registry record reports neither an equivalence margin nor a formal equivalence analysis. It also does not prove that there is no difference. A non-significant p-value is not proof of the null hypothesis, and a confidence interval spanning zero can still include differences that might matter. The record does not identify a threshold for clinical importance.

The secondary outcomes provide additional measurements, but their pattern is mixed and their unadjusted analyses are not accompanied by a reported multiplicity strategy. They should be considered supportive or exploratory context, not decisive evidence that overrides the primary result. The registry record also lacks sufficient analytic detail to determine how the crossover structure was incorporated, how missing data were managed, or what population was analyzed.

These results apply to the reported study population, endpoints, and follow-up described in the registry. They should not be generalized automatically to other patient groups, treatment durations, outcomes, or clinical settings. The trial was recorded as completed, but completion alone does not resolve uncertainty in the posted estimates or the missing analysis details. The findings are statistical descriptions of the registry results and are not medical advice or a treatment recommendation.

17. Why This Trial Matters Statistically

This trial illustrates why a point estimate should be read alongside its uncertainty. The primary mean difference is close to zero, but the confidence interval extends on both sides of zero. Looking only at the point estimate could make the result seem more conclusive than it is; looking only at the p-value would also miss the range of contrasts compatible with the data.

It also illustrates the distinction between a non-significant result and evidence of equivalence. A formal equivalence question requires an explicit margin and an analysis suited to that question. The registry record reports neither, so the primary result cannot support a statistical conclusion that the treatments are equivalent.

The crossover structure makes analysis details particularly important. Because participants were assigned to receive both treatments in different sequences, within-participant dependence and treatment-period patterns may affect the comparison and its precision. The registry record does not explain how the reported means and intervals account for these features. This is a useful reminder that a complete interpretation requires more than knowing the study design label and seeing a summary estimate.

Finally, the presence of several secondary endpoints makes multiplicity relevant. A secondary result that appears notable should be interpreted in the context of the other outcomes and any prespecified testing plan. Since no such plan is reported, the secondary findings have less confirmatory weight. The record therefore demonstrates how uncertainty, design structure, endpoint families, and reporting completeness all shape what can reasonably be concluded from a clinical trial summary.

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 main limitation for statistical interpretation is incomplete reporting of the analysis. The registry entry does not describe the statistical model, whether the crossover observations were analyzed as paired, or whether period and sequence effects were considered. It also does not provide the sponsor’s formal outcome analyses in its analysis listing. As a result, the posted unadjusted comparisons cannot be assessed as a complete analysis of the stated design.

The outcome summaries list n=41 for each treatment group, whereas enrollment is recorded as 48. The registry record does not explain the difference, identify the analysis population, or describe missing-data handling. In a crossover design, incomplete participation or missing measurements may affect whether a within-participant treatment contrast can be estimated, but the record does not say how this was addressed.

The record does not report a multiplicity strategy for the secondary outcomes, or the original sample-size assumptions and justification. The planning illustrations are based on observed effects and should not be mistaken for the trial’s design calculations. The record also does not provide a formal equivalence objective or margin for the primary outcome.

The safety entry lists no affected participants for serious or other adverse events, while deaths are null rather than reported as zero. Further safety details, including timing and ascertainment, are not reported in the registry record. These limitations do not establish that procedures were not conducted; they identify information unavailable in the registry entry and constrain how confidently the posted results can be evaluated.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Investigation of the Athero-Protective Effects of Clopidogrel — NCT01283282.
• Registry record last updated 2015-05-01; status last verified 2015-04.
• Results first posted 2015-05-01.
• 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 describes a completed, randomized, quadruple-masked, crossover Phase 4 study of clopidogrel and placebo in people with coronary artery disease. Enrollment is listed as 48, with the study start recorded as 2008-01 and primary completion as 2010-12. Participants were assigned to a sequence of clopidogrel 75 mg daily and placebo, each for 6 weeks.

The primary endpoint was FMD, reported as percent change in diameter. The posted unadjusted mean difference is 0.08, with a 95% confidence interval from -1.555 to 1.715 and p=0.924. Secondary results cover vascular and inflammatory measures and show a mixed pattern. The registry record does not report the statistical model, analysis population, missing-data approach, or multiplicity plan. The posted findings should therefore be read as summaries with important uncertainty about analysis details.