The ARIES HeartMate 3 Pump IDE Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The ARIES HeartMate 3 Pump IDE Study (NCT04069156), a randomized na study. The primary outcome is Powered Primary Endpoint of Survival Free of Non-surgical Major Hemocompatibility Related Adverse Events.

2. Clinical Question

The central statistical question is about the difference between randomized groups in a composite outcome, not about each component considered separately. A participant counted toward the primary endpoint had to be alive and free of the specified events at the endpoint assessment. The registry reports the number meeting that definition in each group and a sponsor-reported noninferiority analysis. It also permits a simple, unadjusted risk-difference calculation from the posted group counts; that calculation and the sponsor’s analysis do not agree, so the sponsor’s own analysis takes precedence.

The clinical question is narrower than whether aspirin affects every possible outcome after device implantation. The posted primary endpoint combines survival with selected non-surgical events, while bleeding and survival are also among the registry’s secondary outcomes. Findings on those outcomes can add context, but they do not replace the primary endpoint or establish the effect on every individual component.

3. Trial Design

The ARIES HeartMate 3 Pump IDE Study is registered as a randomized, parallel-group clinical investigation in people with heart failure. It compares two antithrombotic regimens in patients treated with the HeartMate 3 left ventricular assist device: vitamin K antagonist with aspirin and vitamin K antagonist with placebo. The registry describes the study as prospective, double-blinded, and placebo-controlled. Its masking field is recorded as quadruple.

The registry lists 628 participants enrolled and identifies Abbott Medical Devices as the sponsor. The study status is completed. The registry gives a start date of 2020-07-14 and a primary completion date of 2023-08-10. Phase is listed as NA. These entries describe the registered study; they do not, by themselves, establish details of how every analysis was conducted.

The primary endpoint is assessed at 12 Months and is reported for the principal analysis population. That population excluded patients with events occurring within 14 days after left ventricular assist device implantation, with the stated purpose of avoiding surgical complications not attributed to treatment. For the primary comparison, the placebo group has 271 participants and 201 meeting the endpoint definition; the aspirin group has 273 participants and 186 meeting it.

The registry also includes adverse-event data for a modified intent-to-treat population, with a different set of group denominators. Secondary results posted in detail include survival and risk of non-surgical bleeding at 24 Months. The registry lists additional secondary outcome categories, including hemorrhagic events, bleeding events, thrombotic events, and stroke. The detailed original statistical analysis plan, including its full approach to missing data and multiplicity, 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.

Before assignment: The intent to treat (ITT) population consisted of all subjects randomized including follow up beyond transition to open label (n=314 in each arm).

Modified Intent-to-Treat (mITT)

Reasons for not completing this period:

Principal Analysis

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The primary end point was analyzed in the principal analysis population, which excluded patients with events occurring within 14 days after LVAD implantation to avoid counting surgical complications not attributed to the treatment.

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: The Modified Intention to Treat Population (mITT) included all randomized subjects with the following exception: 1. Subjects who experienced a surgical adverse event, defined as ≤14 days post-implant, requiring investigator mandated antiplatelet therapy; 2. Subjects who expired, are transplanted, or withdrawn within 14 days of implant.

6. Primary Endpoint

The registry lists the primary outcome as Powered Primary Endpoint of Survival Free of Non-surgical Major Hemocompatibility Related Adverse Events, measured over 12 Months.

The primary endpoint is a composite of survival free of non-surgical major hemocompatibility-related adverse events at 1-year post implant. Its specified event components are stroke, pump thrombosis, major non-surgical bleeding, and arterial peripheral thromboembolism. The registry describes the endpoint as assessed at 12 Months and reports it as a count of participants.

A composite endpoint combines several outcomes into one measure. This can capture more than one clinically important way that treatment-related hemocompatibility problems may arise, while producing a single primary comparison. Here, however, the composite does not reveal by itself which component accounts for the group result. A difference in the composite could reflect one component, several components, or a balance of effects across them. Component-specific results would be needed to distinguish those possibilities; a complete component breakdown for the primary endpoint is not reported in the registry record.

The endpoint also requires survival as well as freedom from the specified events. It therefore differs from a measure that counts only adverse events among people who remain alive, and it differs from survival alone. The primary analysis population excluded events within 14 days after implantation to avoid counting surgical complications not attributed to treatment. That exclusion defines which patients and events contribute to the primary analysis; it should be kept in mind when comparing the primary result with other outcomes reported for a modified intent-to-treat population.

7. Results Posted in the Registry

• Aspirin Arm (Principal Analysis Population): 68.1% (186/273) versus 74.2% (201/271) on control; risk difference -6.0 percentage points (95% CI -13.6 to 1.6), risk ratio 0.92 (0.83–1.02); unadjusted two-proportion z-test p = 0.120.

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.

Survival Rates

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Aspirin Arm (Modified Intent-to-treat Population): 89.8% (263/293) versus 92.9% (275/296) on control; risk difference -3.1 percentage points (95% CI -7.7 to 1.4), risk ratio 0.97 (0.92–1.02); unadjusted two-proportion z-test p = 0.175.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aspirin Arm (Modified Intent-to-treat Population) and the control. The interval gives the range of effects that remain compatible with the data.

Risk of Non-Surgical Bleeding Events

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Aspirin Arm (Modified Intent-to-treat Population): 42.3% (124/293) versus 30.1% (89/296) on control; risk difference 12.3 percentage points (95% CI 4.6 to 20.0), risk ratio 1.41 (1.13–1.75); 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 Aspirin Arm (Modified Intent-to-treat Population) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results add outcome-specific context to the primary composite rather than directly resolving its interpretation. Survival and non-surgical bleeding are reported at 24 Months in the modified intent-to-treat population. These outcomes address distinct aspects of the study question: one describes survival, while the other describes bleeding risk. Their estimates should be interpreted within their own definitions, time frame, and analysis population, not treated as component-level explanations of the primary endpoint.

The pattern across these results is not uniform: the posted survival comparison is less conclusive by its unadjusted confidence interval and p-value, while the non-surgical bleeding comparison has an unadjusted interval above no difference. This contrast emphasizes why a composite primary endpoint and separate secondary outcomes may convey different information. The secondary results do not establish which component drove the primary endpoint, and they do not establish the effect on the other listed secondary outcomes for which detailed results are not included in the registry record.

Unadjusted secondary findings carry less weight as confirmatory evidence because multiple outcomes can be examined and the registry does not report a multiplicity strategy. In general, without an adjustment or prespecified testing hierarchy, nominal p-values do not control the chance of false-positive findings across the family of comparisons. The secondary results are useful for describing the posted pattern and identifying uncertainty, but they should be considered alongside the primary analysis, the analysis-population differences, and the incomplete reporting of the statistical plan.

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

• Rates of Non-surgical Major Hemorrhagic Events
• Rates of Bleeding Events
• Rates of Non-surgical Major Thrombotic Events
• Rates of Stroke
• Survival Rates
• Risk of Non-Surgical Bleeding Events

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference express?

A risk difference compares the proportion of participants meeting an outcome in one group with the proportion in another. It is expressed on an absolute scale: zero corresponds to equal risks, while a positive or negative value indicates which group has the larger observed proportion according to the stated subtraction order. The recalculated primary estimate is defined as aspirin minus placebo, so its negative direction means the observed proportion meeting the endpoint was lower in the aspirin group in this simple calculation. That description is not a conclusion about causation beyond the randomized comparison, nor does it substitute for the sponsor’s analysis.

A risk difference is distinct from a risk ratio or an odds ratio. Those measures compare groups on relative scales, whereas a risk difference represents an absolute separation in proportions. A confidence interval around any of these measures describes uncertainty in the estimate under the statistical method used. Its interpretation depends on the method, analysis population, outcome definition, and assumptions; it is not a range that guarantees the true effect lies within its endpoints.

Why are the primary calculations different?

The posted unadjusted recalculation uses group counts and denominators to estimate a simple risk difference. The sponsor reports a Farrington-Manning risk-difference analysis and identifies it as a noninferiority analysis. These are not interchangeable descriptions: a noninferiority analysis assesses whether the data satisfy a prespecified criterion relative to a margin, while a simple unadjusted difference summarizes the observed group proportions. The margin and detailed analysis specification are not reported in the registry record. Since the posted results are discrepant, the sponsor’s own analysis takes precedence, but the record does not explain the reason for the mismatch.

In general, a noninferiority analysis requires a defined margin and a decision rule specifying how the confidence interval is compared with that margin. The margin represents the largest difference that the study’s design considers acceptable for the noninferiority question. Without the margin and full decision rule, the sponsor’s reported classification cannot be independently reproduced from the registry entry. The reported p-value should therefore be described as the sponsor reports it, rather than reinterpreted using an assumed margin.

What does the composite endpoint mean?

The primary endpoint combines survival and freedom from specified adverse events. Composite endpoints can address a broader clinical question than any one component alone, but they can obscure whether the components occur with similar frequency or carry similar importance. A count of participants meeting the composite does not show how many met each individual component, and the posted primary analysis does not provide a component-by-component comparison. It is therefore important to keep the endpoint definition attached to every interpretation of the primary estimate.

The principal analysis population excludes patients with events occurring within 14 days after implantation. The registry states that this was intended to avoid counting surgical complications not attributed to treatment. Excluding a defined early period changes the population and event experience represented by the primary result. It also means that the primary analysis should not be casually equated with an analysis that includes all events from implantation onward.

What does an unadjusted p-value tell the reader?

A p-value measures how compatible the observed data are with a specified null hypothesis under a statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A smaller p-value can indicate greater incompatibility with the null under that model, but it does not remedy a mismatch in estimand or analysis method. The secondary comparisons are described as unadjusted recalculations; their p-values do not account for testing a collection of outcomes.

Multiplicity arises when several outcomes, time points, or comparisons are examined. In general, examining more hypotheses without an adjustment can increase the chance that at least one result appears statistically notable by chance. Adjustments and testing hierarchies are possible approaches, but the prespecified multiplicity strategy for this trial is not reported in the registry record. Secondary unadjusted p-values should consequently be read as exploratory or descriptive evidence rather than as a complete confirmatory testing framework.

Why do confidence intervals matter?

A confidence interval gives a range of estimates reasonably compatible with the observed data under the chosen method and its assumptions. The interval communicates both direction and precision. If it includes no difference, the data do not exclude equal group risks at the corresponding confidence level; that does not prove equality. If it excludes no difference, that alone does not establish clinical importance, correctness of the model, or control of multiplicity. The width of an interval is informative: wider intervals generally indicate less precision, while narrower intervals indicate greater precision for the specified estimand.

Different confidence-interval procedures can yield different limits, especially when methods target different hypotheses or use different assumptions. The primary recalculation uses a conventional unadjusted risk-difference estimate, whereas the sponsor names a Farrington-Manning method for its noninferiority analysis. Given the discrepancy and incomplete sponsor details in the registry record, their numerical results should not be blended into one estimate.

What can the secondary estimates support?

The registry posts secondary percentages and unadjusted risk-difference calculations for survival and non-surgical bleeding at 24 Months. These describe particular outcomes in the modified intent-to-treat population. They are not adjusted for other outcomes in the registry, and they do not establish a single overall treatment effect. In general, outcome-specific estimates can help identify patterns and uncertainty, but their weight depends on prespecification, missing-data handling, multiplicity, and consistency with the primary question. Those details are not reported in the registry record.

11. Confidence Intervals and Precision

The recalculated primary risk difference is -0.060, with a 95% confidence interval from -0.136 to 0.016. The interval spans values on either side of no difference. This means the unadjusted summary-count analysis is not precise enough to rule out either direction of difference at that confidence level. It does not prove that the groups are equal, and it should not be substituted for the sponsor’s Farrington-Manning noninferiority analysis.

The sponsor reports a 97.5% confidence interval for its risk-difference analysis, with a lower limit of -1.6 and no upper limit reported. Since an upper limit is absent from the registry entry, the reported interval is incomplete for readers attempting to assess its full range. The sponsor’s reported value is 6, and its p-value is < 0.001. The analysis is identified as noninferiority, but the noninferiority margin and the full decision rule are not reported in the registry record. The discrepancy with the recalculation therefore remains unresolved in the registry.

For the posted secondary survival comparison, the recalculated risk difference is -0.031, with a 95% confidence interval from -0.077 to 0.014. Its interval includes no difference and leaves uncertainty about the direction of the group difference. For non-surgical bleeding, the risk difference is 0.122, with a 95% confidence interval from 0.045 to 0.200. That interval lies above no difference under the unadjusted calculation. Neither interval accounts for multiplicity across secondary outcomes.

Confidence intervals describe precision for a specified estimate and method, not certainty about the result. Their interpretation also depends on the population and endpoint: the primary analysis uses the principal analysis population, while these secondary outcomes use the modified intent-to-treat population. The observed precision does not establish that the estimate will generalize beyond the registered study population or resolve limitations in the analysis details.

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 sample-size calculations are planning illustrations based on the observed effect, not the trial’s original design assumptions. The assumptions used for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row asks what would be needed to detect a stated fraction of the observed effect. The rows for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect represent progressively smaller target effects.

For the primary endpoint and the posted secondary outcomes, the figures are participants per arm. The general sample-size note says that time-to-event calculations, when present, instead report total events; these calculations are not time-to-event entries. The 80% power column means the planning calculation targets an 80% chance of detecting the specified effect under its assumptions if that effect were the true one. The 90% power column uses a higher target chance of detection. These are design targets, not guarantees about a future study.

The planning illustrations show that smaller effects require more participants per arm to reach the same target power under the stated assumptions. For example, the primary endpoint illustration gives 883 participants per arm for 80% power at 100% of the observed effect and 3,421 participants per arm for 80% power at 50% of the observed effect. For 90% power, the corresponding figures are 1,182 and 4,579. Such figures depend on treating the observed effect as a planning reference; if the true effect differs, the achieved power would differ as well.

These figures are not observed power. They do not describe the probability that the completed trial’s result is correct, and they do not revise the uncertainty shown by the confidence interval. The trial’s own original design assumptions, including the assumptions used to set its enrollment target, are not reported in the registry record. The planning values should therefore be read as illustrations for hypothetical future designs, not as a reconstruction of the study’s original planning.

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 = 0.742; treatment proportion p₁ = 0.681; average p̄ = 0.712.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6407 = 1.2558.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6393 = 0.5380.
4. n = (1.2558 + 0.5380)² / (-0.0604)² = 882.7, rounded up to 883 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 <- 0.74169741697417                          # control proportion
p1 <- 0.681318681318681                          # 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(4069156)
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 = 883 (80% power), 1,182 (90% power)
 75% of observed effect: n per arm = 1,546 (80% power), 2,069 (90% power)
 50% of observed effect: n per arm = 3,421 (80% power), 4,579 (90% power)
power.prop.test: 882.7 
Simulated power at n = 883 per arm: 0.802 (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 registry reports the sponsor’s primary analysis as a Farrington-Manning risk-difference noninferiority analysis. It gives a risk difference of 6, a lower confidence limit of -1.6 for a 97.5% confidence interval, and p < 0.001. The upper confidence limit is not reported in the registry record. The result is labeled as noninferiority, but the margin and full decision rule are not reported, so the stated conclusion cannot be independently reconstructed from the registry entry alone.

The separate recalculation from the posted counts is an unadjusted aspirin-minus-placebo risk difference of -0.060, with a 95% confidence interval from -0.136 to 0.016 and p = 0.12. This differs materially from the sponsor’s reported result in estimate and inferential presentation. The registry does not explain the discrepancy. Possible explanations must not be guessed from the posted summary.

Because the discrepancy flag is present, the sponsor’s own analysis takes precedence over the recalculation. The recalculation remains a transparent summary of the posted group counts, but it should not be presented as overturning or reproducing the sponsor’s analysis. Readers should keep the two analyses distinct and recognize that the missing noninferiority details limit an independent assessment of the sponsor’s decision.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcome categories, including non-surgical major hemorrhagic events, bleeding events, non-surgical major thrombotic events, stroke, survival, and non-surgical bleeding risk. It reports 12 outcome measures and one analysis. The detailed results included for secondary interpretation concern survival and risk of non-surgical bleeding. The registry does not report a full prespecified testing hierarchy or a multiplicity adjustment strategy. Without that information, it is not possible to determine how the sponsor intended to control the overall false-positive risk across outcomes, time points, or analyses.

In general, multiplicity matters because repeated testing creates more opportunities for apparently notable results even when no corresponding effect exists. A correction, gatekeeping procedure, or hierarchy can address this concern, but none should be attributed to this study without documentation. The unadjusted secondary p-values therefore should not be read as if they were adjusted confirmatory tests. This limitation does not erase the estimates; it affects the strength of claims that can be based on them.

The primary endpoint population excludes patients with events occurring within 14 days after implantation, while adverse-event and posted secondary results use a modified intent-to-treat population. These populations have different definitions and denominators. The registry states the rationale for the primary exclusion but does not report enough detail to assess all consequences of the population definitions or how exclusions were handled across outcomes.

Specific missing-data methods, the amount and pattern of missing outcome data, and sensitivity analyses are not reported in the registry record. The original sample-size justification and full statistical analysis plan are also not reported. These omissions limit assessment of whether the analyses followed their planned procedures, how missing observations may affect estimates, and how the primary and secondary results fit into the intended inferential framework. They are reporting limitations, not evidence by themselves that the results are biased.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: major infection (39.6%), bleeding (34.1%), cardiac arrhythmia (14.9%), cardiac disorders (11.9%), metabolism and nutrition disorders (11.3%).

The adverse-event figures are reported for the modified intent-to-treat population. In the placebo group, the registry lists 296 at risk for serious events, 208 affected by a serious event, and 21 deaths. It lists 200 affected by other events. In the aspirin group, the corresponding entries are 293 at risk, 223 affected by a serious event, 22 deaths, and 181 affected by other events. These are descriptive registry counts, not adjusted comparisons or estimates of causation.

The registry’s listed leading serious-event terms and percentages are Major Infection at 39.6%, Bleeding at 34.1%, Cardiac Arrhythmia at 14.9%, Cardiac Disorders at 11.9%, Metabolism And Nutrition Disorders at 11.3%, and General Disorders And Administration Site Conditions at 10.5%. These terms provide a summary of reported serious events; the registry entry does not provide a group-specific breakdown for these listed percentages. Counts affected by events and deaths should not be added together or assumed to represent mutually exclusive categories.

Safety interpretation requires attention to event definitions, follow-up, population, and whether repeated events are counted. Further detail about those methods is not reported in the registry record. The descriptive figures do not, by themselves, establish that a regimen caused or prevented an event.

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

The registry describes a randomized comparison of aspirin and placebo alongside vitamin K antagonist therapy in people treated with a HeartMate 3 left ventricular assist device. The primary outcome combines survival with freedom from specified non-surgical major hemocompatibility-related events. Its reported group counts and the sponsor’s noninferiority analysis address that defined question, not every possible benefit or harm of the regimens.

The simple recalculation from posted primary counts yields a risk difference whose confidence interval includes no difference, while the sponsor reports a noninferiority analysis with p < 0.001. The results are discrepant, and the reason is not reported in the registry record. The sponsor’s own analysis takes precedence, but the absent upper confidence limit, noninferiority margin, and detailed decision rule restrict independent evaluation. Neither result should be silently substituted for the other.

The secondary results describe survival and non-surgical bleeding at 24 Months in a different analysis population. Their estimates offer additional context, but the registry does not report the multiplicity strategy or enough detail to treat unadjusted secondary results as a complete confirmatory analysis. They also do not identify the primary composite’s component-level pattern.

These findings do not establish an effect on every listed outcome, resolve how missing data were handled, or show how results would apply to populations outside the registered study. Nor do they provide medical advice. Their meaning is limited to the populations, definitions, time frames, and methods recorded, with the noted discrepancy and reporting gaps kept in view.

18. Why This Trial Matters Statistically

This trial raises several important statistical issues in a setting where the primary question is defined by a composite endpoint and a noninferiority analysis. The endpoint combines survival with several major non-surgical events. That allows a single primary comparison, but it also means the overall result cannot show which component contributes most without component-specific reporting. Distinguishing the composite from its components is central to interpreting what the estimate represents.

The primary analysis also illustrates why an estimand and method must be clear. A simple risk difference calculated from posted group counts gives a different result from the sponsor’s Farrington-Manning noninferiority analysis. Because the discrepancy is unresolved and key noninferiority details are absent, readers need to separate the transparent recalculation from the sponsor-reported analysis instead of treating them as interchangeable.

Population definitions matter as well. The primary analysis excludes events within 14 days after implantation, while safety and secondary results use a modified intent-to-treat population. Those choices affect which participants and events are represented in each result. Clear reporting of analysis populations and missing-data procedures is necessary for comparisons across endpoints.

Finally, the secondary outcomes demonstrate the need to interpret multiple results as a family rather than isolating a single unadjusted p-value. A stated multiplicity approach, full analysis plan, and complete component reporting would help readers judge how findings fit together. The registry record’s omissions make these issues particularly relevant to the strength and scope of conclusions that can be drawn.

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.

Several limitations are specific to the available registry record. First, the sponsor’s primary noninferiority result differs from the unadjusted recalculation based on the posted counts. The reason is not reported in the registry record. The sponsor’s analysis takes precedence, but the record omits its upper confidence limit, noninferiority margin, and full decision rule, limiting independent verification.

Second, the primary endpoint is composite, and a complete breakdown of its individual components is not reported. The composite result therefore cannot show whether the observed group pattern reflects stroke, pump thrombosis, major non-surgical bleeding, arterial peripheral thromboembolism, or a combination. The primary population also excludes events occurring within 14 days after implantation, while other posted outcomes use a modified intent-to-treat population.

Third, the detailed secondary results cover only some of the listed secondary outcome categories. The results for the remaining listed outcomes are not reported in the registry record. The posted secondary comparisons are unadjusted, and the multiplicity plan is not reported. Their p-values consequently cannot be interpreted as accounting for the broader set of outcomes.

Finally, missing-data methods, missingness patterns, sensitivity analyses, the original sample-size justification, and the full statistical analysis plan are not reported in the registry record. The adverse-event summaries also do not provide group-specific breakdowns for the listed serious-event term percentages. These reporting gaps limit assessment of robustness and completeness; they should not be replaced with assumptions about the protocol or analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: The ARIES HeartMate 3 Pump IDE Study — NCT04069156.
• Registry record last updated 2025-03-27; status last verified 2025-01.
• Results first posted 2025-03-27.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The ARIES HeartMate 3 Pump IDE Study is a completed randomized, parallel-group study sponsored by Abbott Medical Devices. It compared aspirin 100mg with placebo alongside vitamin K antagonist therapy in people treated with a HeartMate 3 left ventricular assist device. The registry describes the study as prospective, double-blinded, placebo-controlled, and quadruple-masked.

The primary endpoint was survival free of specified non-surgical major hemocompatibility-related adverse events at 12 Months, analyzed in a principal analysis population that excluded events within 14 days after implantation. The sponsor reports a Farrington-Manning noninferiority analysis. A recalculation from posted counts differs, and the sponsor’s own analysis takes precedence.

Secondary results posted in detail include survival and risk of non-surgical bleeding at 24 Months. Interpretation is limited by the unresolved primary discrepancy, incomplete noninferiority details, unreported multiplicity and missing-data methods, and differences between analysis populations.