A Study of Tirzepatide (LY3298176) Compared With Dulaglutide on Major Cardiovascular Events in Participants With Type 2 Diabetes: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Tirzepatide (LY3298176) Compared With Dulaglutide on Major Cardiovascular Events in Participants With Type 2 Diabetes (NCT04255433), a randomized phase 3 study. The primary outcome is Number of Participants From Randomization to First Occurrence of Death From MACE-3 [Composite Endpoint of Major Adverse Cardiovascular Events Death From Cardiovascular Causes, Myocardial Infarction (MI) or Stroke].

2. Clinical Question

3. Trial Design

SURPASS-CVOT was a phase 3, randomized, double-masked, parallel-group trial sponsored by Eli Lilly and Company. The registry reports enrollment of 13299 and a completed status. The study began on 2020-05-29, and primary completion was recorded as 2025-06-12. The planned treatment period was up to 5 years.

Participants were assigned to tirzepatide or 1.5 mg dulaglutide. Tirzepatide began at 2.5 mg once weekly, with escalation by 2.5 mg every 4 weeks to a maximum of 15 mg weekly or a tolerated dose of 5 mg or 10 mg weekly. Dulaglutide was administered at 1.5 mg once weekly. Both were given by subcutaneous injection. The registry describes the study purpose as assessing the efficacy and safety of tirzepatide compared with dulaglutide in people with type 2 diabetes and increased cardiovascular risk.

The primary analysis population was modified intention-to-treat: all randomized participants grouped according to assigned treatment. The primary outcome was the first occurrence of cardiovascular death, myocardial infarction, or stroke. Follow-up for this outcome is described as from randomization through week 259. Participants without a recorded event were censored at their last known contact or at the end of follow-up.

The registry record does not report the original sample-size justification, the trial’s planned statistical analysis, or details of any interim analyses. It also does not report adjusted treatment-effect estimates in the results. These omissions limit how closely the posted unadjusted comparisons can be connected to the trial’s original inferential 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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified Intention-to-treat (mITT) Population included all randomized participants who were grouped according to the treatment assigned at randomization.

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: All randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants From Randomization to First Occurrence of Death From MACE-3 [Composite Endpoint of Major Adverse Cardiovascular Events Death From Cardiovascular Causes, Myocardial Infarction (MI) or Stroke], measured over From randomization (week 0) up to week 259.

The primary endpoint counts participants whose first recorded event was cardiovascular death, myocardial infarction, or stroke. It is a composite: a participant is counted when any one of these components occurs first. The registry describes event timing from randomization and says that participants without an event were censored at their last known contact or the end of follow-up. The stated timeframe runs from randomization through week 259.

Composite cardiovascular endpoints are used to capture several important types of cardiovascular event in one outcome. In general, combining components can make an overall endpoint more informative than considering only one event type, especially when the events are related to the clinical question. But a composite does not mean its components are equally frequent or carry equal clinical importance. A difference in the composite can be influenced more by some components than others, so component results should be considered separately where they are reported.

The posted primary result is a number of participants with an event and an unadjusted risk difference. It is not a hazard ratio, and it does not express how quickly events occurred or account for their timing in the same way as a time-to-event model. The registry record describes the endpoint in time-to-event terms, but the posted comparison gives the event counts and risk difference rather than a model-based estimate of event timing.

7. Results Posted in the Registry

• 1.5 mg Dulaglutide: 13.1% (862/6579) versus 12.2% (801/6586) on control; risk difference 0.9 percentage points (95% CI -0.2 to 2.1), risk ratio 1.08 (0.98–1.18); unadjusted two-proportion z-test p = 0.104.

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.

Number of Participants From Randomization to Time to Occurrence of All-Cause 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:
  • 1.5 mg Dulaglutide: 10.2% (669/6579) versus 8.6% (566/6586) on control; risk difference 1.6 percentage points (95% CI 0.6 to 2.6), risk ratio 1.18 (1.06–1.32); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for 1.5 mg Dulaglutide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants From Randomization to Time of Occurrence of 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:
  • 1.5 mg Dulaglutide: 6.2% (408/6579) versus 5.6% (367/6586) on control; risk difference 0.6 percentage points (95% CI -0.2 to 1.4), risk ratio 1.11 (0.97–1.28); unadjusted two-proportion z-test p = 0.125.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 1.5 mg Dulaglutide and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants From Randomization to Time to First Occurrence of Myocardial Infarction (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:
  • 1.5 mg Dulaglutide: 5.4% (357/6579) versus 4.7% (311/6586) on control; risk difference 0.7 percentage points (95% CI -0.0 to 1.5), risk ratio 1.15 (0.99–1.33); unadjusted two-proportion z-test p = 0.066.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 1.5 mg Dulaglutide and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the clinical questions beyond the primary composite, including all-cause death, cardiovascular death, myocardial infarction, stroke, revascularization, heart-failure events, and nephropathy. Among the numerical secondary comparisons reported, the observed risk differences have a consistent direction, with higher event proportions in the dulaglutide group. Their uncertainty is not uniform: the all-cause death interval does not include zero, whereas the cardiovascular death and myocardial infarction intervals do.

These results add context to the primary composite but do not establish that every component or related outcome differs between groups. The primary endpoint combines event types, and component-specific comparisons can be less precise than a composite comparison because each concerns a narrower outcome. Conversely, a composite result should not be assumed to be driven by every component in the same way. The record does not report numerical results for every listed secondary endpoint, so no broader pattern across all secondary outcomes can be concluded from the outcomes listed alone.

Secondary comparisons generally carry less confirmatory weight when many outcomes are examined without a reported multiplicity procedure. If many tests are considered, some may appear notable by chance even when there is no underlying difference. The registry record does not report multiplicity adjustment or a hierarchy for the secondary outcomes. Their estimates should therefore be interpreted as descriptive and considered alongside the primary result, rather than as independent proof of treatment effects. They do not override the uncertainty in the primary comparison.

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

• Number of Participants From Randomization to Time to Occurrence of All-Cause Death
• Number of Participants From Randomization to Time of Occurrence of CV Death
• Number of Participants From Randomization to Time to First Occurrence of Myocardial Infarction (MI)
• Number of Participants From Randomization toTime to First Occurrence of Stroke
• Number of Participants From Randomization to Time to First Occurrence of the Expanded Composite of CV Death, MI, Stroke or Coronary Revascularization (MACE-4)
• Number of Participants From Randomization to Time to First Occurrence of CV Deaths or Heart Failure Events Requiring Hospitalization and/or Urgent Heart Failure Visits
• Number of Participants From Randomization to Time to First Occurrence of Revascularization
• Number of Participants From Randomization to Time to First Occurrence of New or Worsening Nephropathy

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary for the posted count comparison: each participant is either counted as having experienced the composite event during follow-up or is not counted as having experienced it. The endpoint itself combines cardiovascular death, myocardial infarction, and stroke. The registry also describes when an event occurred and how participants without an event were censored, which are time-to-event features. However, the posted effect estimate is a risk difference based on event proportions, not a time-to-event model estimate.

What does the risk difference compare?

The risk difference is the event proportion in the dulaglutide group minus the event proportion in the tirzepatide group. A positive estimate means the observed proportion was higher in the first group named in that contrast; a negative estimate means it was lower. A value of zero represents no difference in the proportions. The estimate is unadjusted, so it is a direct comparison of the posted group-level event proportions rather than an estimate adjusted for other participant characteristics or time-to-event modeling.

Risk differences are expressed on an absolute scale. In general, they answer how far apart the observed event proportions are, rather than how many times larger one is than the other. This makes the result relatively direct to interpret, but the meaning still depends on the outcome definition, follow-up, population, and uncertainty around the estimate. A risk difference does not show whether the difference is statistically reliable by itself; the confidence interval and analysis context are also needed.

How should the confidence interval be read?

A confidence interval describes the uncertainty around an estimated effect under the statistical method used. In general, a 95% confidence interval is produced by a procedure that, across repeated samples under its assumptions, would cover the underlying effect 95% of the time. It is not a statement that there is a 95% probability that this particular interval contains the true effect. For the primary risk difference, the interval runs from -0.002 to 0.021. Because zero lies within that range, the posted data are compatible with no difference as well as with values on either side of zero.

The unadjusted p-value is 0.104. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. Here it should be considered alongside the estimate and confidence interval. The registry record does not report an adjusted p-value or a model-based primary treatment effect.

Why do event counts and censoring matter?

The primary result reports the number of participants with an event, while the endpoint description also specifies follow-up time. Participants without a recorded event are censored at their last known contact or the end of follow-up. In general, censoring means that a participant contributes information up to a known point without being counted as having experienced the event after that point. A time-to-event analysis can use the timing of events and censoring; a simple event proportion does not use that timing in the same way. The posted risk difference therefore should not be interpreted as a comparison of event rates or of time until an event.

The record does not state additional missing-data procedures, such as how any other unavailable endpoint information was handled. It also does not report the assumptions or analysis details needed to assess whether censoring was treated in a way that matches the trial’s planned statistical method. No assumptions about these procedures should be inferred from the event counts alone.

What do the secondary comparisons add?

The reported secondary outcomes use the same broad idea of comparing participant event proportions between groups. Each outcome is a separate question, and their estimates need not have the same precision or represent the same clinical event. Secondary comparisons can help describe the pattern across outcomes, but interpreting many outcomes increases the chance that some findings look notable by chance alone. In general, multiplicity procedures address this by controlling the error associated with making multiple inferences. The registry record does not report whether such a procedure was planned or used.

For this reason, the secondary p-values and intervals should be treated as unadjusted descriptive evidence unless the registry record documents an appropriate confirmatory plan. The record lists 13 secondary outcomes, but only some have numerical comparisons described in the available results. It does not report a complete adjusted analysis across these outcomes. A favorable direction on one secondary measure does not establish a broad effect across all of them.

What do the planning calculations represent?

Planning illustrations use the observed effect as a starting point and consider smaller fractions of that effect. In general, power is the probability that a specified analysis will detect an effect of a stated size under its assumptions. A planned power target is not evidence that the observed result has that probability of being correct. The planning calculations for this study are illustrations rather than the trial’s original design justification, which is not reported in the registry record. They should not be confused with an observed power calculation or with the actual inferential analysis of the trial.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.009, and its 95% confidence interval extends from -0.002 to 0.021. The interval includes zero, so the observed data do not pin down a single direction of difference with high precision. Values below zero and above zero remain within the interval. The posted p-value of 0.104 is consistent with this uncertainty, but the interval conveys more than a threshold-based decision: it shows the range of effects that remain compatible with the analysis.

Precision depends in part on the number of observed events and the variability of the data. In general, a confidence interval is narrower when an estimate is more precise and wider when it is less precise. The primary endpoint combines several event types, and the posted count comparison does not include an adjusted time-to-event estimate. The interval therefore describes uncertainty for the reported risk-difference comparison, not uncertainty for every possible treatment-effect measure.

The confidence interval should not be read as a range of likely individual outcomes or as proof that effects outside it are impossible. It also does not establish equivalence: the registry record does not report an equivalence margin or a non-inferiority analysis. Interpretation should remain tied to the specified endpoint, population, and unadjusted comparison. The secondary endpoint intervals vary in whether they include zero, and their individual precision does not remove the multiplicity concern or establish a consistent effect across 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 illustrate how many participants per arm might be required under stated assumptions to detect effects at different fractions of the observed effect. For a binary participant-count endpoint such as the primary comparison, the figures are participants per arm. For a time-to-event calculation using the Schoenfeld method, figures refer instead to the total number of events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect.

The 80% power column represents a planning target under which, if the assumed effect were the true effect and the calculation assumptions held, the design would detect that effect in 80% of repeated studies. The 90% power column uses a higher detection probability under the same kind of assumptions. These are planning targets, not guarantees for an individual study. Smaller effects are harder to distinguish from random variation, so the calculations require more participants per arm when the target is a smaller fraction of the observed effect.

The values are planning illustrations calculated from the observed effect, not the trial’s original design justification; that justification is not reported in the registry record. They are not observed power. They also do not establish that a future study will have the stated performance: the assumptions about allocation, significance level, approximation, and effect size would need to be appropriate for that future 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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.122; treatment proportion p₁ = 0.131; average p̄ = 0.126.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4698 = 0.9208.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4698 = 0.3954.
4. n = (0.9208 + 0.3954)² / (0.0094)² = 19,600.4, rounded up to 19,601 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 <- 0.121621621621622                          # control proportion
p1 <- 0.131022951816385                          # 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(4255433)
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 = 19,601 (80% power), 26,239 (90% power)
 75% of observed effect: n per arm = 34,569 (80% power), 46,277 (90% power)
 50% of observed effect: n per arm = 77,154 (80% power), 103,286 (90% power)
power.prop.test: 19600.4 
Simulated power at n = 19,601 per arm: 0.800 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary cardiovascular composite and multiple secondary outcomes. It does not report a statistical plan describing a hierarchy among those outcomes, a family of hypotheses, or a multiplicity adjustment. When several statistical tests are conducted, the chance of at least one result appearing notable by chance can increase. In general, multiplicity procedures are designed to address that issue, but the record does not say whether any were used. The reported secondary p-values should therefore be regarded as unadjusted rather than as a set of confirmatory findings.

The primary comparison itself is also presented as an unadjusted risk difference. The registry record does not report an adjusted estimate, the covariates that might have been used in an adjusted model, or further details of the primary statistical analysis. The stated population is modified intention-to-treat, with randomized participants analyzed according to assigned treatment. That population definition is reported, but the registry record does not describe additional analysis populations or sensitivity analyses.

The primary endpoint definition states that participants without an event were censored at their last known contact or the end of follow-up. This gives a basic description of how event-free follow-up was handled. It does not specify other missing-data methods, the amount of missing endpoint information, or assumptions about censoring. Those details are not reported in the registry record.

The original sample-size justification, planned interim analyses, and broader statistical analysis plan are also not reported. As a result, the posted unadjusted comparisons cannot be checked against a documented confirmatory testing strategy in the record. This does not show that such methods were absent from the trial; it means they are not reported in the registry record.

15. 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: pneumonia (2.4%), acute kidney injury (1.4%), covid-19 (1.3%), covid-19 pneumonia (1.0%), peripheral arterial occlusive disease (1.0%).

The registry lists serious adverse events for groups with 6647 participants at risk in each group. Serious adverse events affected 2117 participants in the tirzepatide group and 2121 in the dulaglutide group. The counts of other adverse events were 4718 and 4297, respectively, among groups with 6647 at risk. Deaths listed in the adverse-event data were 568 and 670, respectively. These are counts, not adjusted comparisons, and the registry data do not establish that a treatment caused an event or difference.

Frequently listed serious-event terms include pneumonia (2.4%), acute kidney injury (1.4%), Covid-19 (1.3%), Covid-19 pneumonia (1.0%), peripheral arterial occlusive disease (1.0%), and angina unstable (0.9%). Such terms describe recorded events; they do not by themselves provide a complete comparison of the event’s seriousness, duration, relationship to treatment, or clinical course. The registry record does not report an adjusted safety analysis in the results. Counts should be interpreted within the registry’s reporting context, not as a stand-alone estimate of comparative risk.

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

The primary result is a comparison of observed event proportions for the first occurrence of cardiovascular death, myocardial infarction, or stroke in the modified intention-to-treat population. The point estimate is positive for the dulaglutide-minus-tirzepatide risk difference, but the 95% confidence interval includes zero. The posted result therefore leaves uncertainty about the direction and size of the underlying difference under this analysis.

This does not establish that the treatments are equivalent, and it does not establish a clear difference. Equivalence or non-inferiority requires a prespecified margin and an analysis designed to test that question; those details are not reported in the registry record. Nor does a non-significant unadjusted p-value prove that the treatments have identical effects. The estimate and its uncertainty are more informative than a binary label based only on a p-value.

The result is specific to the endpoint, follow-up description, and analysis population recorded for this trial. It does not show whether the pattern is the same for each component of the composite, for every secondary outcome, or for participant subgroups. The record lists a range of secondary outcomes, but numerical findings for all of them are not reported. The posted unadjusted analysis also does not answer every possible time-to-event question, because it presents a risk difference rather than a model-based estimate of event timing.

Safety counts provide additional descriptive information but do not, by themselves, identify treatment causation or establish a comparative safety profile. A complete interpretation would consider the study’s prespecified analyses, outcome definitions, missing-data handling, and safety methods; some of these details are not reported in the registry record. The statistics describe the posted data and their uncertainty, not an individualized prediction or a treatment recommendation.

17. Why This Trial Matters Statistically

This trial raises statistical questions that are common in cardiovascular outcome research: how to compare treatments using a composite endpoint, how to interpret an absolute risk difference, and how much certainty to attach to a point estimate when its confidence interval includes zero. The primary comparison is not simply a contest between event counts. It is an estimate with uncertainty, tied to a defined population, endpoint, and follow-up approach.

The composite endpoint combines cardiovascular death, myocardial infarction, and stroke. That can make a broad cardiovascular question more tractable, but interpretation still depends on the components. The secondary comparisons offer some component-level context, while their unadjusted status and the lack of reported multiplicity methods constrain how strongly they can be interpreted. The distinction between a composite result and its component outcomes is therefore central to reading this record.

The registry also illustrates the difference between a trial’s original design and retrospective planning illustrations based on an observed effect. The latter can show how assumed effect size and target power relate to required sample size, but they do not reveal the original design rationale or the probability that the observed result is correct. Here, the original justification is not reported in the registry record.

Finally, the primary result is posted as a risk difference even though the endpoint description includes time-to-event features and censoring. Keeping the estimand clear matters: event proportions and event timing answer related, but not identical, questions. Reading the estimate, confidence interval, endpoint definition, and analysis limitations together supports a more measured interpretation than relying on a single threshold.

18. Limitations

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

Several limitations are specific to the posted record. The primary comparison is an unadjusted risk difference based on participant event counts. Although the endpoint definition describes time to event and censoring, the results do not include a hazard ratio or other model-based estimate that uses event timing. The posted effect therefore should not be extended to conclusions about how quickly events occurred.

The confidence interval for the primary risk difference includes zero, leaving uncertainty about the direction and magnitude of the difference. The record does not report a prespecified equivalence or non-inferiority margin, so the result cannot be interpreted as demonstrating equivalence. It also does not report the original sample-size rationale, planned analysis details, interim analyses, or a multiplicity approach for secondary outcomes.

The registry lists several secondary endpoints, but numerical results for all of them are not reported in the registry record. The reported secondary comparisons are unadjusted, and the record does not document a strategy for interpreting multiple tests. There is also no subgroup analysis described in these results, so the average comparison should not be assumed to apply identically across participant groups.

For missing information, the primary endpoint description says participants without an event were censored at last known contact or the end of follow-up. Other missing-data procedures and the amount of unavailable endpoint information are not reported in the registry record. The displayed adverse-event counts are descriptive and do not establish causation or replace a comparative safety analysis. These limitations reflect what is reported in the registry record, not proof that additional analyses were not conducted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of Tirzepatide (LY3298176) Compared With Dulaglutide on Major Cardiovascular Events in Participants With Type 2 Diabetes — NCT04255433.
• Registry record last updated 2026-07-08; status last verified 2026-06.
• Results first posted 2026-07-08.
• 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

SURPASS-CVOT was a completed phase 3, randomized, double-masked, parallel-group trial sponsored by Eli Lilly and Company. The registry reports enrollment of 13299 participants with type 2 diabetes and increased cardiovascular risk. The comparison was tirzepatide, titrated to a maximum tolerated dose, versus 1.5 mg dulaglutide, with both treatments administered once weekly for up to 5 years.

The primary outcome counted participants with a first occurrence of cardiovascular death, myocardial infarction, or stroke through week 259. In the modified intention-to-treat population, the posted unadjusted risk difference was 0.009, with a 95% confidence interval from -0.002 to 0.021 and an unadjusted p-value of 0.104. The interval includes zero, so the posted primary comparison remains uncertain about the direction and size of the difference. The registry record does not report the original sample-size justification, multiplicity strategy, or a complete adjusted analysis.