Comparative Efficacy of Ticagrelor Versus Aspirin on Blood Viscosity in Peripheral Artery Disease Patients With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparative Efficacy of Ticagrelor Versus Aspirin on Blood Viscosity in Peripheral Artery Disease Patients With Type 2 Diabetes (NCT02325466), a randomized phase 3 study. The primary outcome is Mean Change in Low Shear Blood Viscosity.

2. Clinical Question

3. Trial Design

The registry describes a randomized, triple-masked, phase 3 crossover trial, marked completed. Enrollment is listed as 70. The trial concerned peripheral artery disease in people with type 2 diabetes and compared aspirin, ticagrelor, and their combination.

According to the study summary, participants were randomized into 3 groups, and each group was to receive each of the 3 treatments over the course of the crossover study. Each treatment period lasted 4 weeks. The three regimens were aspirin 81 mg daily with ticagrelor placebo twice daily; aspirin 81 mg daily with ticagrelor 90 mg twice daily; and aspirin placebo daily with ticagrelor 90 mg twice daily. The record does not describe the treatment order, any washout periods, or how period and carryover effects were addressed.

The primary outcome is mean change in low-shear blood viscosity, with the timeframe listed as baseline and week 16. The population description says data were included for participants who returned for any of their visits. Secondary outcomes listed in the record concern mean change in peripheral arterial blood flow and a microvascular blood-flow composite score. Although 4 outcome measures are listed, detailed results for only the primary outcome are included in the record summarized by these results. A full statistical analysis plan, including details of the masking procedures and analysis population, is 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.

Period 1 Timeframe - Baseline to Week 4

Reasons for not completing this period:

Period 2 - Timeframe Week 4 to Week 10

Reasons for not completing this period:

3rd Crossover - Week 10 to Week 16

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: data collected and included for any participants who return for any of their visits.

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 Mean Change in Low Shear Blood Viscosity, measured over baseline, week 16.

Low-shear blood viscosity is the primary continuous endpoint. The record expresses it in 5 s^-1 cPs and defines the outcome as mean change, comparing baseline with week 16. The study summary describes measuring viscosity at low and high shear rates at the end of each 4 week treatment period; the posted primary outcome specifically concerns low shear.

Viscosity is a property of how blood flows, and measuring it at a specified shear rate gives a defined laboratory outcome for comparison across treatment conditions. In general, a mean change condenses participants’ paired baseline and follow-up measurements into an average change. That average can be compared between treatment regimens, while the spread around each mean describes how varied the recorded changes were.

The rationale in the registry is to compare the effect of aspirin-ticagrelor and ticagrelor alone with aspirin on blood viscosity. The record does not give a threshold for a clinically important difference or explain how a change in this laboratory measure should be interpreted in relation to patient-important outcomes. Therefore, the endpoint supports a statistical comparison of measured viscosity changes; by itself, it does not establish the importance of any difference for health or symptoms.

7. Results Posted in the Registry

• Aspirin/Ticagrelor: mean -1.79 versus 1.04 on control; difference -2.84 (95% CI -3.44 to -2.24), standardized effect d = -1.68; z-test p = <0.001.
• Aspirin Placebo/Ticagrelor: mean -1.76 versus 1.04 on control; difference -2.80 (95% CI -3.31 to -2.29), standardized effect d = -1.98; z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is a continuous measure, and the registry reports its mean and standard deviation for each treatment condition. A mean is the arithmetic average of the recorded changes. A standard deviation describes how dispersed the individual recorded values are around that average; it is not the uncertainty interval for the mean and does not show the full shape of the data distribution.

What does a mean difference represent?

A mean difference subtracts one group’s average from another’s. The reference condition is aspirin with ticagrelor placebo. The reported differences compare each ticagrelor-containing regimen with that condition. A negative estimate means the first-listed regimen’s posted mean change is lower numerically than the reference mean change. It does not, without a clinically meaningful threshold and endpoint interpretation, tell whether the contrast matters to patients.

The comparisons include interval bounds and unadjusted p-values. A p-value assesses how compatible the observed comparison is with a null hypothesis of no difference, under the statistical assumptions used. It is not a measure of effect size, and it does not express the probability that the null hypothesis is true. Here, each posted unadjusted p-value is p < 0.001. The record does not identify a multiplicity adjustment or detail the test used in a sponsor analysis.

Why does the crossover design matter?

In a crossover design, participants receive more than one treatment condition. Each participant can therefore contribute measurements under multiple conditions, making treatment comparisons potentially paired rather than independent. In general, accounting for this pairing can improve precision when the measurements from the same participant are related. Treatment order, period effects, and carryover can also affect interpretation, so suitable analyses often need to consider the design and timing.

The registry summary says that each group was to receive each of the 3 treatments, with each treatment period lasting 4 weeks. The posted comparison statistics include treatment-condition sample sizes and pooled standard deviations, but the registry does not state how the crossover dependence was handled in its original analysis. The unadjusted comparisons recalculated from summary statistics should consequently be read as summary-based contrasts, not as a substitute for a fully specified crossover model.

What can the spread tell us?

The standard deviations show that participant-level changes varied within each condition. Variation matters because an average alone can conceal heterogeneous responses or unusual observations. General statistical practice also considers distributional assumptions and influential observations when analyzing continuous outcomes. The registry does not report distribution checks, transformations, or sensitivity analyses for this endpoint.

Over-dispersion is a general concern when observed variability exceeds what a model assumes. If a model underestimates variability, its uncertainty estimates can be too narrow. The posted standard deviations describe observed spread, but the record does not provide the model diagnostics needed to judge whether any specific variance assumption was appropriate.

What do the interval bounds add?

An interval estimate expresses uncertainty around an estimated effect. In general, a wider interval indicates less precision, while a narrower interval indicates more precision under the model’s assumptions. The posted bounds for both comparisons lie below zero. The confidence level and exact construction method are not reported in the registry record, so those details cannot be used to make a more specific assessment of coverage or calibration.

The posted calculations are unadjusted recalculations from summary statistics, and the discrepancy flag is false. They are useful for describing the contrast in the posted group means, but they do not reveal whether the trial’s original analysis used covariate adjustment, participant-level pairing, period terms, or other model features. Those details are not reported in the registry record.

How should the analysis population be understood?

The primary outcome description includes data collected for participants who returned for any of their visits. That wording indicates that the available outcome data were used, but it does not specify a complete-case rule, an intention-to-treat population, or a per-protocol population. Nor does it explain how missing visits or incomplete treatment periods were handled. Since crossover analyses rely on information across treatment conditions, the extent and pattern of missing measurements can affect the comparison. The registry record does not report missing-data methods or participant flow by period.

10. Confidence Intervals and Precision

The estimated mean difference for aspirin-ticagrelor versus aspirin alone is -2.838, with reported interval bounds from -3.439 to -2.237. For ticagrelor alone versus aspirin alone, the estimate is -2.804, with bounds from -3.314 to -2.294. Both interval ranges are entirely below zero, matching the direction of the estimated mean differences. The registry record does not report the confidence level or the method used to construct these intervals.

Interval width is one way to judge precision: a narrower range generally allows a more concentrated set of effect values than a wider range, conditional on the method’s assumptions. The two reported ranges have similar spans, but precision should not be judged from width alone. The uncertainty calculations may depend on the statistical model, the crossover pairing, and how missing observations were handled. Those analytic details are not reported in the registry record.

The standard deviations also show considerable spread in individual changes relative to the group means, but they are not confidence intervals. The reported observations differ by treatment condition, and the primary outcome description includes participants who returned for any visits. Without fuller information on paired observations and missingness, the summary statistics cannot establish how much information contributed to each within-person treatment contrast.

The unadjusted p-values are p < 0.001 for both comparisons. Small p-values do not replace interval estimates: they address compatibility with a null difference under the test assumptions, whereas intervals show a range of estimates compatible with the data and method. Neither provides a direct measure of clinical importance. A threshold for a meaningful change is not reported in the registry record.

11. 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 sample-size figures are planning illustrations based on the observed effect, not observed power. The entries are participants per arm, not total event counts. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These are planning assumptions for the illustration; the trial’s own original design assumptions are not reported in the registry record.

The column for 80% power gives the number of participants per arm estimated to be needed for an 80% chance of detecting the specified effect under those planning assumptions, if the assumed effect and model conditions hold. The 90% power column gives the corresponding planning number for a 90% chance. These probabilities describe a proposed study design under assumptions; they do not describe the probability that the posted result is true.

Rows that plan for 100% of the observed effect use the full estimated difference as the effect to detect. Rows planning for 75% or 50% use smaller effects. Smaller effects are harder to distinguish from random variation and therefore require more participants per arm in these illustrations. For example, the aspirin-ticagrelor comparison lists 6 participants per arm for 80% power at 100% of the observed effect, and 23 participants per arm at 50%. The ticagrelor-only comparison lists 5 participants per arm at 100% and 17 at 50%. The planning figures should be interpreted as conditional illustrations, not as a reconstruction of the trial’s design rationale.

12. 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 = -2.838; pooled standard deviation σ = 1.688.
2. n = 2 × (1.96 + 0.842)² × 1.688² / -2.838² = 5.6, rounded up to 6 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 <- -2.838                      # observed difference in means
sigma <- 1.68843166002899                     # 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(2325466)
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 = 6 (80% power), 8 (90% power)
 75% of observed effect: n per arm = 10 (80% power), 14 (90% power)
 50% of observed effect: n per arm = 23 (80% power), 30 (90% power)
power.t.test: 6.7 
Simulated power at n = 6 per arm: 0.745 (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.

13. Multiplicity, Missing Data and Analysis Populations

The record lists one primary endpoint, mean change in low-shear blood viscosity, and two secondary outcomes: mean change in peripheral arterial blood flow and mean change in a microvascular blood-flow composite score. It also lists 4 outcome measures. The posted findings summarized by these statistics give comparisons for the primary endpoint, while results for the secondary outcomes are not reported in the registry record.

Testing more than one outcome or treatment contrast creates a multiplicity issue. In general, the more statistical tests considered, the greater the chance that at least one apparently notable result arises by chance if no adjustment or hierarchy is used. The record does not report whether the trial specified a testing hierarchy, adjusted p-values, or another multiplicity strategy. The posted p-values are unadjusted, so they should not be read as accounting for all outcomes and comparisons.

Missing-data handling is also not described in detail. The primary outcome population is described as data collected and included for participants who returned for any of their visits. The treatment-condition observations differ in count, but the registry does not explain missing visits, incomplete periods, exclusions, imputation, or sensitivity analyses. It does not report whether the analysis population was intention-to-treat, per-protocol, or defined by another rule.

These omissions matter in a crossover study because measurements from multiple treatment conditions may be linked within the same participant. The record does not state how within-participant correlation, treatment order, period effects, or carryover were modeled. The original statistical plan and analysis details are not reported in the registry record, so it is not possible to assess whether the posted comparisons reflect a prespecified analysis or how missingness and multiplicity were addressed.

14. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: gi bleeding (1.4%).

The registry reports serious adverse events separately for each treatment condition. For aspirin with ticagrelor placebo, 70 were listed at risk and 0 serious adverse events were reported. For aspirin with ticagrelor, 70 were listed at risk and 1 serious adverse event was reported. For aspirin placebo with ticagrelor, 70 were listed at risk and 0 serious adverse events were reported. Deaths were reported as 0 for each condition.

The record lists GI Bleeding at 1.4% among the top serious adverse-event terms. It does not provide enough detail to assign that term to a specific treatment condition from the listed figures. The other adverse-event counts were 0, 0, and 1 across the three conditions in the order above.

These are registry counts, not proof that a treatment caused or prevented an event. The crossover design also means the same participant may have received more than one treatment condition, and the record does not describe attribution rules, event timing, exposure duration, or statistical comparisons for safety. The figures therefore describe what was reported, not comparative safety certainty.

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

The posted primary outcome results show lower mean changes numerically for both ticagrelor-containing regimens than for aspirin alone. The unadjusted mean differences are -2.838 for aspirin-ticagrelor and -2.804 for ticagrelor alone, each with p < 0.001. The reported interval bounds for both contrasts are below zero. These findings describe the recorded low-shear blood-viscosity changes in the analyzed observations.

They do not establish that either regimen changes symptoms, peripheral blood flow, clinical events, or longer-term health outcomes. Although the registry lists blood-flow outcomes as secondary measures, their results are not reported in the registry record. The record also does not give a threshold for a clinically important viscosity change. Statistical evidence of a difference is not the same as evidence that the difference matters clinically.

The results should also be interpreted in light of the crossover design and incomplete analysis information. The record does not report the statistical model, treatment sequence, handling of period or carryover effects, or missing-data methods. The unadjusted summary comparisons do not reveal how those design features may affect the original analysis. The confidence level for the interval bounds is not reported either.

Safety counts are limited in scope and cannot establish comparative risk. The listed serious adverse events and deaths describe registry reporting for the treatment conditions; they do not establish causality or rule out events that were not recorded in these summaries. Overall, the posted data support a statistical description of one laboratory endpoint, while leaving clinical importance, other outcomes, and several analysis details unresolved.

16. Why This Trial Matters Statistically

This trial raises a useful statistical issue: a crossover comparison can collect measurements under several treatment conditions from the same participants. That structure can make paired comparisons informative, but it also means the analysis should reflect within-participant relationships and treatment timing. The registry describes the crossover arrangement but does not report enough model detail to assess how those features were handled.

The endpoint is a continuous laboratory measurement, reported as mean change in low-shear viscosity. Its group means and standard deviations offer a direct summary of average changes and their variability. The unadjusted differences and interval bounds add information about the direction and uncertainty of the contrasts, while leaving clinical relevance dependent on a meaningful-change threshold that is not reported.

The record also illustrates why statistical significance should not be read in isolation. Both unadjusted p-values are p < 0.001, but the registry does not report a multiplicity strategy, analysis model, or results for the listed secondary outcomes. Those omissions constrain assessment of how the primary result fits into the study’s full set of questions.

Finally, the trial’s adverse-event figures and outcome summaries have different roles. A laboratory endpoint can describe a measurable biological difference, while safety counts describe reported events; neither alone supplies a complete account of clinical outcomes. Reading the estimates alongside their precision, design, missing-data context, and reporting limits gives a more faithful statistical interpretation than relying on a p-value alone.

17. 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 details needed to interpret the crossover comparisons are not reported in the registry record. The treatment sequence, washout arrangements, and methods for handling period or carryover effects are unspecified. The record also does not describe whether the statistical model accounted for the fact that each participant was intended to receive all 3 treatments. This limits evaluation of the unadjusted comparisons from group summary statistics.

The primary outcome description includes participants who returned for any visits, but missing observations and incomplete treatment periods are not characterized. There is no reported participant flow by treatment period, missing-data method, or sensitivity analysis. The analysis population is not identified as intention-to-treat, per-protocol, or another defined set.

Although the registry lists secondary blood-flow outcomes and 4 outcome measures, those outcome results are not reported in the registry record summarized by these findings. The multiplicity strategy, original analysis plan, and confidence level for the interval bounds are also not reported. No clinically meaningful threshold for the viscosity endpoint is given.

The safety summary provides counts by treatment condition but does not describe event attribution, timing, or exposure-specific analysis. It should not be used to infer causation or comparative risk. These limitations do not change the posted numerical summaries, but they restrict conclusions about robustness, clinical importance, and how well the analysis reflects the planned crossover design.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Comparative Efficacy of Ticagrelor Versus Aspirin on Blood Viscosity in Peripheral Artery Disease Patients With Type 2 Diabetes — NCT02325466.
• Registry record last updated 2022-03-21; status last verified 2022-03.
• Results first posted 2022-03-21.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT02325466 is a randomized, triple-masked, phase 3 crossover trial marked completed, with enrollment listed as 70. It studied people with peripheral artery disease and type 2 diabetes and compared aspirin alone, ticagrelor alone, and aspirin with ticagrelor.

The primary outcome was mean change in low-shear blood viscosity between baseline and week 16, reported in 5 s^-1 cPs. The posted unadjusted mean differences versus aspirin alone were -2.838 for aspirin-ticagrelor and -2.804 for ticagrelor alone; both p-values were p < 0.001. The record lists peripheral arterial blood flow and a microvascular blood-flow composite as secondary outcomes, but their results are not reported in the registry record.

Serious adverse-event counts and deaths are reported by treatment condition. Important details about the original analysis, missing-data handling, crossover effects, and multiplicity are not reported in the registry record.