A Study Comparing Cardiovascular Effects of Ticagrelor Versus Placebo in Patients With Type 2 Diabetes Mellitus: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study Comparing Cardiovascular Effects of Ticagrelor Versus Placebo in Patients With Type 2 Diabetes Mellitus (NCT01991795), a randomized phase 3 study. The primary outcome is Composite of Cardiovascular (CV) Death, MI or Stroke.

2. Clinical Question

3. Trial Design

THEMIS was a randomized, double-blind, placebo-controlled, parallel-group, phase 3 trial sponsored by AstraZeneca. The registry lists multinational conduct and quadruple masking. The study compared ticagrelor with placebo in people with type 2 diabetes mellitus. Enrollment was 19271. The record lists ticagrelor 60 mg and ticagrelor placebo as the interventions.

The arm descriptions note that ticagrelor 90 mg or corresponding placebo was initially selected, then reduced to ticagrelor 60 mg or corresponding placebo in Clinical Study Protocol Amendment No 1. The registry record does not report the reason for the change, its timing relative to participant enrollment, or any further implementation details.

The study started on 2014-02-10, had primary completion on 2019-01-25, and is marked completed. The primary endpoint was assessed from randomization to the primary analysis censoring date. Median time in study until that censoring date was 40 months. This is a median follow-up description, not a claim that every participant was followed for the same length of time.

For the primary analysis, the full analysis set excluded 51 patients who were randomized to study drug at a site prematurely closed by the sponsor. The two posted event-count groups were 9619 for ticagrelor and 9601 for placebo; those group counts correspond to the outcome record, while the analysis-population description specifies the site-based exclusion. The registry record does not report the original sample-size justification, detailed allocation procedures, or the full statistical analysis plan.

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: Enrolled patients randomised to study drug 95.8%; n =19271, of which 51 patients were randomised to study drug at a site prematurely closed by sponsor and excluded from the study results. Patients who were not randomised 4.2%; n=837. Patient did not meet inclusion/exclusion criteria n=454, Patient decision n=256, Death n=1, Other reason n=131.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The population was the full analysis set, which included all randomised patients except the 51 patients who were randomised to study drug at a site prematurely closed by sponsor.

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: Of the 19271 patients randomised to study drug, 51 patients were randomised to study drug at a site prematurely closed by sponsor and excluded from the study results. 19220 were included in the evaluation of study results.

6. Primary Endpoint

The registry lists the primary outcome as Composite of Cardiovascular (CV) Death, MI or Stroke, measured over From randomisation to primary analysis censoring date (PACD). Median time in study until PACD was 40 months..

The primary endpoint was a composite of cardiovascular death, myocardial infarction or stroke, recorded as the number of participants with an event. A composite endpoint combines several clinically distinct outcomes into one analysis. It can capture whether any component occurred and can provide a single primary comparison, but its overall result does not show that every component changed in the same way. The component outcomes therefore need separate consideration, while keeping in mind that they are secondary analyses.

The registry describes follow-up from randomization to the primary analysis censoring date. For a participant without an event, censoring occurred at the earliest of the primary analysis censoring date, the last endpoint assessment date and the non-cardiovascular death date. This specifies how follow-up ended for the primary endpoint; it does not mean a censored participant had an event.

A time-to-event analysis uses information about when events occurred and how long participants were observed, rather than treating everyone as if they had identical follow-up. The sponsor’s reported primary method was Cox regression, with a hazard ratio as its effect measure. The event counts and simple recalculations describe the posted counts and group risks; they are not a substitute for the time-to-event analysis. Median time in study until the primary analysis censoring date was 40 months.

The record does not report a separate rationale for selecting this particular composite, nor does it describe how the endpoint components were weighted. In the posted definition, each listed event type contributes to the composite when it meets the endpoint definition.

7. Results Posted in the Registry

• Ticagrelor 60 mg: 7.7% (736/9619) versus 8.5% (818/9601) on control; risk difference -0.9 percentage points (95% CI -1.6 to -0.1), risk ratio 0.90 (0.82–0.99); unadjusted two-proportion z-test p = 0.027.

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.

CV Death

• 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:
  • Ticagrelor 60 mg: 3.8% (364/9619) versus 3.7% (357/9601) on control; risk difference 0.1 percentage points (95% CI -0.5 to 0.6), risk ratio 1.02 (0.88–1.17); unadjusted two-proportion z-test p = 0.810.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ticagrelor 60 mg and the control. The interval gives the range of effects that remain compatible with the data.

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:
  • Ticagrelor 60 mg: 2.8% (274/9619) versus 3.4% (328/9601) on control; risk difference -0.6 percentage points (95% CI -1.1 to -0.1), risk ratio 0.83 (0.71–0.98); unadjusted two-proportion z-test p = 0.024.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Ticagrelor 60 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Ischaemic Stroke

• 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:
  • Ticagrelor 60 mg: 1.6% (152/9619) versus 2.0% (191/9601) on control; risk difference -0.4 percentage points (95% CI -0.8 to -0.0), risk ratio 0.79 (0.64–0.98); unadjusted two-proportion z-test p = 0.032.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Ticagrelor 60 mg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes provide a mixed component-level pattern around the primary composite. The reported cardiovascular-death hazard ratio is 1.02, while the reported hazard ratios for myocardial infarction and ischaemic stroke are 0.84 and 0.80. Thus, the primary composite’s overall direction is not shared uniformly by every reported component. This is one reason a composite result should not be read as evidence that each included event type had the same association.

The component analyses help describe the endpoint pattern, but they are secondary to the primary composite question. A component typically has fewer events than a composite, and its estimate can consequently be less precise. Differences among component estimates may reflect real variation, sampling variability, or both; the registry record alone does not establish which explanation accounts for the pattern.

The registry lists all-cause death as a secondary outcome, but a result for that outcome is not reported in the registry record. The record lists 9 outcome measures and 9 analyses, but does not state how these secondary analyses were organized for confirmatory inference. In particular, multiplicity adjustment, a testing hierarchy and control of the overall false-positive rate are not reported in the registry record.

Unadjusted secondary p-values carry less weight when several outcomes are examined, because repeated testing increases the chance of at least one apparently notable result under a collection of null effects. This general concern does not mean the component results are uninformative; rather, they are best treated as supportive and descriptive unless a prespecified multiplicity strategy is documented. Their relationship to the primary outcome is informative, but they cannot independently establish the overall trial conclusion.

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

• CV Death
• MI
• Ischaemic Stroke
• All-cause Death

9. Statistical Interpretation

10. Statistical Methods Explained

What does the hazard ratio describe?

The registry reports Cox regression for the primary outcome and gives a hazard ratio. In general, a hazard is the instantaneous event rate among participants who have not yet had the event, at a particular point in follow-up. A hazard ratio compares those rates between groups over follow-up as represented by the model. A value of 1 corresponds to equal hazards under that comparison; a value below 1 indicates a lower estimated hazard in the intervention group, and a value above 1 indicates a higher estimated hazard. This is a relative time-to-event measure, not a risk difference or a count of events prevented.

The primary reported hazard ratio was 0.90, with a 95% confidence interval from 0.81 to 0.99. The Cox method uses event timing and accommodates differing follow-up through censoring. The registry gives the censoring rule for participants without an event, including the primary analysis censoring date, last endpoint assessment date and non-cardiovascular death date. Details of model diagnostics, covariate adjustment and whether assumptions were assessed are not reported in the registry record.

How do event counts differ from a time-to-event analysis?

The posted outcome counts state how many participants had an event in each group. They are useful for understanding the observed event burden and for simple unadjusted comparisons. A count-based comparison does not, by itself, incorporate when each event occurred or how long each participant remained under observation. The Cox analysis does incorporate timing and censoring as defined for the endpoint. As a result, a hazard ratio and a simple risk comparison answer related but not identical statistical questions.

The primary event counts were 736 among 9619 participants in the ticagrelor group and 818 among 9601 in the placebo group. The recalculated risk comparison is an unadjusted calculation from these posted summaries. It should not be described as an adjusted model result or as the sponsor’s analysis. The registry reports no discrepancy flag between the recalculation and sponsor analysis.

What does a confidence interval convey?

A confidence interval gives a range of values compatible with the data and the statistical procedure, under its assumptions. It conveys uncertainty around an estimate; it is not a range in which every possible true value is equally likely, and it does not capture every possible source of bias or error. The primary 95% interval extends from 0.81 to 0.99 for the hazard ratio. Because the interval is near 1 at its upper end, the estimate is more informative when presented with the interval than as a simple label alone.

A p-value assesses compatibility between the observed data and a specified null hypothesis, given the model and assumptions. It does not measure the probability that the null hypothesis is true, the size or importance of an effect, or the chance that results will replicate. The registry reports p-values for the sponsor analyses and recalculated unadjusted comparisons. The p-values for secondary outcomes should be read in light of the number of analyses and the absence of reported multiplicity procedures.

Why distinguish the primary and secondary analyses?

The primary endpoint is the main stated outcome for the trial and its reported analysis is the central inferential result. Secondary outcomes can help describe which components or related outcomes contributed to the pattern, but multiple analyses increase the opportunity for apparently notable findings by chance. The registry lists secondary outcomes for cardiovascular death, myocardial infarction, ischaemic stroke and all-cause death. It reports posted analyses for the first three; an all-cause death result is not reported in the registry record.

The available secondary results are Cox-model hazard ratios, whereas the recalculated comparisons use event counts. These outcomes are related to the composite, but they are not interchangeable. A component result can differ from the composite because it concerns fewer events and a narrower endpoint. The record does not report whether secondary outcomes were adjusted for multiplicity, ordered in a testing hierarchy, or designated as confirmatory.

What does the planning illustration mean?

Sample-size estimates based on an observed effect are planning illustrations, not evidence of the trial’s original design rationale. In general, power is the probability that a planned analysis will detect a specified effect under assumed conditions if that effect is true. The illustration uses a two-sided significance level of 0.05, equal allocation, a normal approximation, and effects set at stated fractions of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

For the count-based outcomes, the planning figures are participants per arm. The illustration includes planning for 100%, 75% and 50% of the observed effect, with estimates for 80% and 90% power. A smaller target effect generally requires more participants to detect under otherwise comparable assumptions. These planning calculations do not describe the achieved power of the completed trial and should not be interpreted as observed power.

11. Confidence Intervals and Precision

The primary Cox estimate is a hazard ratio of 0.90, with a 95% confidence interval from 0.81 to 0.99. The interval gives a sense of the statistical precision of the estimate under the reported analysis. Its range is consistent with estimates below 1, while the upper limit is close to 1. Reporting the estimate and interval together makes the uncertainty more visible than stating only that the registry classified the analysis as superiority.

Confidence intervals do not include all uncertainty. They reflect sampling variability under a statistical method and its assumptions, but they do not automatically account for outcome misclassification, selection, unreported analytic choices or multiplicity. The registry record does not report enough information to assess all such issues. The interval should therefore be understood as precision for the stated Cox analysis, not as a complete measure of certainty about every interpretation.

The event counts provide another view of the data: 736 participants had the composite event in the ticagrelor group and 818 in the placebo group. Those counts do not convey event timing or the follow-up duration for each person. The reported Cox interval and any unadjusted interval for a count-based comparison therefore refer to different measures and should not be treated as interchangeable.

The secondary hazard-ratio intervals are wider for some outcomes, including cardiovascular death, for which the reported interval is 0.88 to 1.18. The reported intervals for myocardial infarction and ischaemic stroke are 0.71 to 0.98 and 0.64 to 0.99, respectively. These component estimates are less decisive on their own than a primary result because they are secondary and because the registry does not report multiplicity adjustment. Precision is not the same as clinical importance, and an interval alone does not establish how an effect would apply to an individual.

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 estimates for these event-count outcomes are expressed as participants per arm, not as a total across both groups. They use a two-sided significance level of 0.05, equal allocation between the arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect: planning for 100%, 75% or 50% of that effect. For a time-to-event planning calculation, the stated general convention is to report the total number of events using the Schoenfeld method; the posted count-based outcomes use participants per arm.

The 80% power column describes a planning scenario with an 80% probability of detecting the target effect under the stated assumptions, if that effect is real and the assumptions hold. The 90% power column uses a higher target probability of detection, which generally requires a larger planned sample. These values are not counts observed in the trial. For example, primary-endpoint planning for 100% of the observed effect gives 15,469 participants per arm for 80% power and 20,708 participants per arm for 90% power. Planning for 75% of the observed effect gives 27,837 per arm for 80% power and 37,265 per arm for 90% power. For 50% of the observed effect, the corresponding estimates are 63,389 and 84,859 per arm.

Smaller effects are harder to distinguish from random variation, so detecting a smaller target effect generally requires more participants under otherwise similar assumptions. These estimates are planning illustrations based on the observed effect, not the trial’s original sample-size rationale. The original design assumptions are not reported in the registry record. This is not observed power.

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 = 0.085; treatment proportion p₁ = 0.077; average p̄ = 0.081.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3855 = 0.7556.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3855 = 0.3244.
4. n = (0.7556 + 0.3244)² / (-0.0087)² = 15,468.4, rounded up to 15,469 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 <- 0.0851994583897511                          # control proportion
p1 <- 0.0765152302734172                          # 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(1991795)
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 = 15,469 (80% power), 20,708 (90% power)
 75% of observed effect: n per arm = 27,837 (80% power), 37,265 (90% power)
 50% of observed effect: n per arm = 63,389 (80% power), 84,859 (90% power)
power.prop.test: 15468.4 
Simulated power at n = 15,469 per arm: 0.794 (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. Analyses Reported by the Sponsor

The sponsor’s primary analysis is a Cox regression with a hazard ratio of 0.90 and a 95% confidence interval from 0.81 to 0.99. The registry classifies it as a superiority analysis. A separate simple recalculation from the posted primary event counts is an unadjusted comparison of group risks, not a reproduction of the Cox model. The recalculated comparison points in the same direction as the sponsor’s result, but the measures differ because one uses event timing and censoring while the other uses summarized counts.

The record does not flag a discrepancy between the recalculation and the sponsor analysis. The sponsor’s reported analysis remains the primary result to use when describing the trial’s inferential finding; a simple recalculation is useful as a check and as a way to interpret the posted counts, but it does not replace the prespecified model result. The registry does not report enough detail about model covariates or diagnostics to independently reconstruct the sponsor’s Cox analysis from the posted summaries.

The same distinction applies to secondary outcomes. Their posted Cox hazard ratios are the sponsor-reported time-to-event results, while count-based recalculations are unadjusted summaries. They can support descriptive comparison, but they do not supersede the registry analyses or address the additional uncertainty from multiple secondary tests.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several statistical hypotheses are tested. Even when each individual test uses a conventional threshold, conducting multiple tests raises the chance that at least one will appear notable by chance if all corresponding null hypotheses are true. This is especially relevant when a trial reports a composite primary endpoint alongside component and other secondary outcomes.

The registry lists secondary outcomes for cardiovascular death, myocardial infarction, ischaemic stroke and all-cause death. It reports analyses for cardiovascular death, myocardial infarction and ischaemic stroke; an all-cause death result is not reported in the registry record. Although the record lists 9 outcome measures and 9 analyses, the multiplicity strategy, testing hierarchy and any adjustment to secondary p-values are not reported in the registry record. Consequently, secondary results should not be treated as if they were independent confirmatory tests with a documented family-wise error strategy.

The primary endpoint population is described as the full analysis set, including all randomized patients except the 51 randomized to study drug at a site prematurely closed by the sponsor. The registry provides the primary endpoint censoring rule for participants without an event. It does not report the extent or handling of missing endpoint assessments, whether any imputation was used, or sensitivity analyses for missing data. It also does not report details about the original sample-size justification, interim analyses, or the full analysis plan. Those omissions limit assessment of how every analysis decision was prespecified and how robust the estimates are to alternative assumptions.

These are limits of what can be established from the registry record, not evidence that a particular method was or was not used. The reported Cox analyses and their confidence intervals remain the record’s stated results, but interpretation of secondary tests and missing-data robustness requires caution where the relevant procedures are not reported.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: angina unstable (4.2%), angina pectoris (2.6%), acute myocardial infarction (2.1%), pneumonia (1.5%), ischaemic stroke (1.2%).

The registry reports serious adverse events and other adverse events separately. In the ticagrelor group, 3049 participants were listed as affected by serious adverse events among 9562 at risk; in the placebo group, the corresponding figures were 3210 among 9531. For other adverse events, the counts were 1951 among 9562 at risk with ticagrelor and 610 among 9531 at risk with placebo. Deaths were reported as 589 and 602, respectively. These are registry safety counts and denominators, not a causal comparison adjusted for follow-up or participant characteristics.

The most frequent listed serious terms included unstable angina at 4.2%, angina pectoris at 2.6%, acute myocardial infarction at 2.1%, pneumonia at 1.5%, ischaemic stroke at 1.2% and coronary artery disease at 0.9%. A listed adverse event does not by itself establish that the study drug caused it. The record does not provide a detailed account of event definitions, exposure-adjusted rates, severity beyond the serious-event category, or statistical comparisons. These figures should be read as reported safety summaries, not as a stand-alone assessment of benefit and harm.

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

The registry’s primary Cox analysis estimates a lower event hazard for the composite of cardiovascular death, myocardial infarction or stroke in the ticagrelor group than in the placebo group. The hazard ratio was 0.90, with a 95% confidence interval from 0.81 to 0.99. This is a group-level time-to-event estimate under the reported model. It does not mean that every participant had a lower risk, nor does it predict an individual outcome.

The result concerns the composite as defined in the registry and the analyzed population, which excluded 51 patients randomized at a prematurely closed site. It does not establish that all three components changed in the same direction. The component analyses show differing estimates, and their secondary status and unreported multiplicity handling make them less conclusive on their own. The median time in study until the primary analysis censoring date was 40 months, but individual follow-up was not necessarily identical.

The result also does not by itself quantify an absolute effect for a particular person, establish a mechanism, or resolve how results vary across groups not described in the registry record. The record does not report subgroup findings, a detailed account of missing endpoint data, or the original sample-size justification. The adverse-event summaries are descriptive and do not establish causation.

Statistical evidence should be interpreted with the estimate, its interval, the endpoint definition, analysis population and study design in view. The primary analysis is the central reported result, while secondary outcomes and simple recalculations can add context without replacing it. Nothing in these registry statistics constitutes medical advice or a recommendation about treatment for an individual.

18. Why This Trial Matters Statistically

THEMIS illustrates why the analysis method and endpoint definition matter. The primary endpoint is a composite, while the sponsor’s reported analysis is a Cox model that uses event timing and censoring. The event counts offer an accessible description of how many participants experienced an event, but they do not contain all the information used by a time-to-event analysis. Comparing these measures without distinguishing them can lead to an inaccurate reading of the result.

The case also shows why a composite result needs component-level context. The primary hazard ratio is below 1, while the cardiovascular-death estimate is above 1 and estimates for the other reported components are below 1. The overall composite describes the endpoint as a whole; it cannot be assumed to apply identically to every component. Component analyses are also affected by the number of events and by multiplicity.

Finally, statistical precision and evidential strength are not interchangeable. The primary confidence interval conveys uncertainty around the reported estimate, and the unreported details of multiplicity, missing data and model diagnostics limit what can be independently assessed. Planning estimates based on the observed effect can illustrate how sample requirements change with target effect size, but they do not reveal the trial’s original design rationale or achieved power. These distinctions make the registry results more interpretable without overstating what they establish.

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 registry record leaves several trial-specific details unavailable. It does not report the original sample-size justification or design assumptions, the full statistical analysis plan, interim analyses, model diagnostics, covariate adjustment details, or the reason and timing for the dose reduction from 90 mg to 60 mg. These gaps limit reconstruction of the planned analyses and assessment of how closely the posted analyses followed the original plan.

The primary population excluded 51 randomized patients at a site prematurely closed by the sponsor. The record identifies the exclusion but does not report sensitivity analyses evaluating its consequences. It also does not report the extent of missing endpoint assessments, how any missing data were handled, or the results of analyses under alternative missing-data assumptions. The endpoint censoring rule is reported, but that does not answer every question about incomplete follow-up.

The composite combines cardiovascular death, myocardial infarction and stroke, which are distinct outcomes. The overall estimate therefore does not describe each component independently. The reported component analyses are secondary, and the registry does not report a multiplicity strategy. The all-cause death outcome is listed, but its result is not reported in the registry record.

Safety summaries are counts and listed terms rather than a complete causal or exposure-adjusted assessment. The registry record does not report enough detail in these summaries to assess event timing or make adjusted comparisons. These limitations qualify interpretation of the posted results; they do not, by themselves, demonstrate bias or invalidate the reported primary analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study Comparing Cardiovascular Effects of Ticagrelor Versus Placebo in Patients With Type 2 Diabetes Mellitus — NCT01991795.
• Registry record last updated 2020-03-18; status last verified 2020-03.
• Results first posted 2020-03-18.
• 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

THEMIS was a completed, randomized, double-blind, placebo-controlled, parallel-group phase 3 trial sponsored by AstraZeneca. It compared ticagrelor 60 mg with placebo in people with type 2 diabetes mellitus. Enrollment was 19271. The primary endpoint was a composite of cardiovascular death, myocardial infarction or stroke, assessed from randomization to the primary analysis censoring date; median time in study until that date was 40 months.

The registry’s primary Cox analysis reported a hazard ratio of 0.90, with a 95% confidence interval from 0.81 to 0.99. The full analysis set excluded 51 patients randomized at a prematurely closed site. Secondary results show differing component estimates, and multiplicity adjustment is not reported in the registry record. The record also does not report the original sample-size rationale or detailed missing-data procedures.