TReatment of Atrial Fibrillation With Dual dEfibrillator in Heart Failure Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for TReatment of Atrial Fibrillation With Dual dEfibrillator in Heart Failure Patients (NCT00345592), a randomized phase 4 study. The primary outcome is Unplanned Hospital Admissions for Cardiac Reasons OR Death of Cardiovascular Causes OR Progression to Chronic Atrial Fibrillation.

2. Clinical Question

The clinical question is about the treatment strategy, not simply whether a device was implanted: both arms are described with the same dual implantable defibrillator, while the approach to delivering therapy for atrial arrhythmias differs. The registry’s brief summary frames the comparison as automatic electrical therapy against an in-hospital approach for symptomatic atrial tachycardia and fibrillation. It also describes the intended population as patients with congestive heart failure who had an indication for CRT defibrillator implantation.

The primary outcome combines events that differ in nature: an unplanned hospital admission for a cardiac reason, cardiovascular death, and progression to chronic atrial fibrillation. A composite can capture more than one kind of clinically relevant outcome, but a combined result does not by itself show which component accounts for the observed pattern. Component-specific primary outcome results are not reported in the registry record. The record also does not give additional details about how each component was defined or adjudicated.

3. Trial Design

NCT00345592 is listed as a completed Phase 4 randomized trial with a parallel-group design and no masking. The registry records an enrollment of 420. The primary outcome results list 199.0 participants in the Device Managed Arm and 197.0 in the Traditional Arm; these are the group denominators reported with the outcome, not a replacement for the registry’s overall enrollment figure. Participant flow and reasons for any difference between the enrollment and outcome denominators are not reported in the registry record.

The intervention is described as a dual (atrial and ventricular) implantable defibrillator in each arm. The distinction is the delivery strategy for atrial-arrhythmia therapy. In the device-managed arm, the device delivers shock therapy automatically. In the traditional arm, a physician commands therapy in a hospital environment. The intervention listing repeats the same device name, but the record’s arm descriptions provide the relevant comparison between treatment strategies.

The condition listed is congestive heart failure. The registry describes the intended population as patients with a CHF indication for implantation of a CRT defibrillator. More detailed eligibility criteria, recruitment sites, the randomization procedure, allocation concealment, and the schedule of follow-up assessments are not reported in the registry record. The trial is marked completed; its recorded start is 2006-10 and its primary completion is 2012-11.

The primary outcome is recorded as a participant count for the composite of cardiac-related unplanned hospital admissions, cardiovascular death, or progression to chronic atrial fibrillation, with a timeframe of 3 years from randomization (39 months total). One outcome measure and one analysis are listed. The record does not report an analysis method for the sponsor’s hazard ratio, nor does it describe the original sample-size justification or a prespecified statistical analysis plan. Those details should not be inferred from the results or from the separate planning illustrations.

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: 24 subjects were not randomized: * 7 died before randomization (causes: 3 cardiac, 2 non-cardiac, 2 unknown); * 7 voluntarily withdrew; * 5 withdrawn due to AF. * 2 had device explanted before randomization; * 1 had biventricular pacing turned OFF * 1 was withdrawn from the study for inclusion criteria violation; * 1 lost to follow up.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Unplanned Hospital Admissions for Cardiac Reasons OR Death of Cardiovascular Causes OR Progression to Chronic Atrial Fibrillation, measured over 3 years from randomization (39 months total).

The primary endpoint counts participants who experienced at least one of the listed outcomes: an unplanned hospital admission for a cardiac reason, death from cardiovascular causes, or progression to chronic atrial fibrillation. The registry gives the measurement unit as participants and the timeframe as 3 years from randomization (39 months total). Results are reported as event counts in each arm.

A composite endpoint combines multiple outcomes into one measure. In general, this can represent a broader clinical question than any single component alone and can capture events of different kinds during follow-up. It also means the overall result should be read as a result for the combined endpoint. Without component-level results, it is not possible to determine from the composite counts how many participants experienced each specific component or which component contributed most to the overall pattern. Such component-level results are not reported in the registry record.

The two outcome counts are 43.0 in the Device Managed Arm and 44.0 in the Traditional Arm. These counts are reported against group denominators of 199.0 and 197.0, respectively. They describe the posted outcome results, but the record does not provide further detail on event adjudication, how participants with more than one component were counted, or how missing follow-up information was handled. These endpoint details matter when interpreting a composite because the operational definitions and analysis rules determine precisely what a reported event count represents.

7. Results Posted in the Registry

• Traditional Arm: 22.3% (44/197) versus 21.6% (43/199) on control; risk difference 0.7 percentage points (95% CI -7.4 to 8.9), risk ratio 1.03 (0.71–1.50); unadjusted two-proportion z-test p = 0.861.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: the registry reports whether participants experienced the composite event during the stated follow-up period. The arm-level results are counts, paired with the denominators used for those results. For a binary outcome, a risk is the proportion of participants with the event in a group. A risk difference compares those group risks by subtraction, retaining an absolute scale. Positive and negative values indicate opposite directions according to the comparison’s stated arm ordering; a value of zero corresponds to equal observed risks.

What does the risk difference describe?

The unadjusted re-calculation compares the Traditional Arm with the Device Managed Arm and reports a risk difference of 0.007. Its 95% confidence interval runs from -0.074 to 0.089. Because this interval crosses zero, the data are compatible with a negative difference, no difference, or a positive difference within the interval. This does not mean those possibilities are equally likely, and it does not establish that the strategies are equivalent. The registry does not report an equivalence margin or a non-inferiority margin.

The re-calculation is unadjusted: it uses the posted summary counts rather than participant-level data or a model adjusting for other variables. It is therefore a simple comparison of the observed group results. A recalculated estimate can be useful for understanding the counts, but it does not replace a sponsor analysis that uses a different statistical approach. No discrepancy is flagged between the two results in the registry record.

How does a confidence interval help?

A confidence interval describes the uncertainty around an estimate under the assumptions of the method used. In general, a 95% confidence procedure would produce intervals containing the target parameter in 95% of repeated samples if the model assumptions held. It is not a statement that there is a 95% probability that this particular interval contains the true value. A wide interval indicates limited precision: the data do not pin down the contrast closely. The risk-difference interval crosses its no-difference value, while the sponsor’s hazard-ratio interval crosses its no-association value.

Why are there several effect measures?

The record includes a re-calculated risk difference and also lists risk-ratio and odds-ratio estimates. A risk ratio compares the event risks in two groups as a ratio. An odds ratio compares event odds, rather than risks, and can be less intuitive when the event is not rare. These measures answer related but distinct questions and have different null values: zero for a difference and one for a ratio. Their numerical scales should not be treated as interchangeable. The risk-ratio and odds-ratio confidence intervals listed in the record each span their respective null value, so they also do not isolate a single direction of association.

The sponsor analysis reports a hazard ratio (HR), with a 95% confidence interval. In general, a hazard ratio compares the instantaneous event rates between groups among participants who have not yet had the event, within a time-to-event model. It uses information about event timing and may account for censoring, depending on the model and analysis rules. Those rules, including the model specification and censoring approach, are not reported in the registry record. A hazard ratio is not simply the ratio of the final event counts or of the observed risks.

What does the p-value say?

The unadjusted p-value is 0.861. In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, a measure of clinical importance, or a measure of the chance that the result will replicate. A large p-value does not prove the absence of an effect. It should be read alongside the estimated contrast and its confidence interval, which show the range of effect sizes compatible with the analysis.

The sponsor’s hazard-ratio analysis has no p-value reported in the registry record. The record also does not report the method used for that analysis. The sponsor estimate and the unadjusted re-calculation should therefore be presented as distinct analyses, not combined into a single statistic or treated as if they used identical methods. General statistical interpretation can explain the measures, but it cannot fill in the missing analysis specifications.

Why does the composite endpoint matter?

Combining events into a composite can increase the number of participants contributing an event to the overall endpoint and address a broader question. At the same time, components can differ in clinical meaning, frequency, and importance. If component results are absent, an overall composite estimate cannot reveal whether its pattern is driven by one component or reflects a similar pattern across all components. The registry reports the composite counts but does not report component-specific counts or effects.

The results are not an adjusted comparison of baseline characteristics, and no such adjustment is described. The registry record gives only summary outcome data and a sponsor-reported HR. Any general explanation of binary outcomes, effect measures, confidence intervals, and p-values should be distinguished from the unreported details of the trial’s own statistical plan.

10. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate the comparison, not whether an estimate is statistically significant by itself. The re-calculated risk difference is 0.007, with a 95% confidence interval from -0.074 to 0.089. The interval includes zero and extends in both directions, so the posted summary data do not confine the absolute difference to one direction. Its width also indicates that the point estimate should not be mistaken for a highly exact estimate of the group contrast.

The sponsor’s hazard ratio is 0.987, with a 95% confidence interval from 0.684 to 1.503. For a hazard ratio, one is the null value. The interval includes values below and above one, allowing different possible directions of association under the reported measure. It is not a narrow interval around the estimate. The registry record does not give the sponsor’s modeling details, which limits a fuller assessment of the interval’s assumptions.

Confidence intervals reflect sampling uncertainty under the method’s assumptions. They do not account automatically for every possible source of uncertainty, such as missing outcome data, measurement differences, or analytic choices. The registry record does not report missing-data procedures, event adjudication details, or the sponsor model specification. The reported intervals should therefore be interpreted as uncertainty under their respective analyses, not as a complete accounting of every limitation.

The intervals do not demonstrate equivalence or prove that a meaningful difference is absent. Such conclusions require prespecified criteria and suitable analyses, which are not reported in the registry record. The point estimates are close to their respective null values, but precision is judged from the full interval as well as the estimate. Both intervals leave substantial uncertainty about the size and direction of the comparison.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. They are planning illustrations computed from the observed effect, rather than the trial’s original design calculation. The 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 set as a stated fraction of the observed effect. The original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the planned number of participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are design probabilities under a specified model and effect size; they do not describe the probability that the observed result is correct.

For planning at 100% of the observed effect, the figures are 50,921 participants per arm for 80% power and 68,168 participants per arm for 90% power. For planning at 75% of the observed effect, they are 90,257 participants per arm for 80% power and 120,828 participants per arm for 90% power. For planning at 50% of the observed effect, they are 202,470 participants per arm for 80% power and 271,050 participants per arm for 90% power. The pattern illustrates a general planning principle: smaller effects require more participants to detect under otherwise unchanged assumptions.

These figures are not observed power. They are illustrative calculations based on the observed estimate and the stated assumptions, not evidence that the trial was designed around those targets. In particular, the original design assumptions, target effect, and sample-size justification are not reported in the registry record. The figures should be read as hypothetical planning requirements, not as a retrospective judgment of whether the trial succeeded.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.216; treatment proportion p₁ = 0.223; average p̄ = 0.220.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5856 = 1.1477.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5855 = 0.4928.
4. n = (1.1477 + 0.4928)² / (0.0073)² = 50,920.2, rounded up to 50,921 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 <- 0.21608040201005                          # control proportion
p1 <- 0.223350253807107                          # 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(345592)
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 = 50,921 (80% power), 68,168 (90% power)
 75% of observed effect: n per arm = 90,257 (80% power), 120,828 (90% power)
 50% of observed effect: n per arm = 202,470 (80% power), 271,050 (90% power)
power.prop.test: 50920.2 
Simulated power at n = 50,921 per arm: 0.801 (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.

13. Analyses Reported by the Sponsor

The sponsor-reported analysis gives a hazard ratio of 0.987, with a 95% confidence interval from 0.684 to 1.503. This is a time-to-event summary, whereas the re-calculation is an unadjusted risk difference based on the posted participant counts. The two estimates use different scales and may reflect different analytic methods, so they should not be expected to be numerically identical.

The sponsor interval includes one, the null value for a hazard ratio. The re-calculated risk-difference interval includes zero, its null value. Both intervals allow values on either side of their respective nulls. The re-calculation also reports an unadjusted p-value of 0.861. No p-value is reported for the sponsor’s HR in the registry record.

The sponsor’s analysis takes precedence as the trial’s own analysis; the re-calculation is a simple, unadjusted check using posted summary results. No discrepancy is flagged in the registry record. The model, analysis population, covariate adjustment, and handling of censoring for the sponsor analysis are not reported in the registry record. Without those details, the HR cannot be fully reconstructed or compared on identical assumptions with the count-based re-calculation. The registry does not establish that the two analyses answer precisely the same statistical question.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome measure and one analysis, with no secondary outcome measures posted. The primary measure is itself a composite of unplanned hospital admissions for cardiac reasons, death of cardiovascular causes, or progression to chronic atrial fibrillation. The record does not provide separate primary results for those components. It also does not describe additional exploratory analyses or a hierarchy of endpoints.

Multiplicity arises when many hypotheses or outcomes are tested: without an appropriate strategy, the chance of at least one false-positive finding can increase. The registry record does not report a multiplicity adjustment, testing hierarchy, or other plan for managing multiple comparisons. Because no secondary results are posted, the record does not support an assessment of how multiple outcome testing was handled beyond the listed primary result. The existence of a single listed analysis should not be taken as proof that no other analyses were conducted.

Missing-data procedures are not reported in the registry record. The outcome denominators are 199.0 for the Device Managed Arm and 197.0 for the Traditional Arm, but the record does not explain participant flow, missing outcome status, censoring, exclusions, or the reasons these analysis denominators differ from the registry enrollment of 420. It is not possible to determine from the posted details whether all randomized participants were included in the primary analysis or how incomplete follow-up was treated.

The analysis populations are also not described. The record does not say whether the primary comparison followed an intention-to-treat population, a per-protocol population, or another prespecified group. Allocation concealment and the randomization implementation are not reported. The statistical method for the sponsor’s hazard-ratio analysis is not reported, and the original analysis plan is not available in the registry record. These missing details prevent a complete audit of the prespecified analysis and its implementation.

15. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hopspitalizatin/intervention (39.2%), worsening of cardiac disorders (8.0%), worsening of unknown conditions leading to death (6.5%), worsening of non-cardiac disorders (5.1%), atrial fibrillation (5.0%).

The registry reports serious adverse events affecting 103 of 199 participants in the Device Managed Arm and 93 of 197 participants in the Traditional Arm. It also reports other adverse events affecting 39 of 199 and 22 of 197 participants, respectively. These are arm-level counts as recorded; they are not the primary composite endpoint results. Serious adverse events and other adverse events are separate categories in the registry data and should not be combined with the primary outcome counts.

The listed serious adverse event terms include hospitalization/intervention (spelled as “hopspitalizatin/intervention” in the registry record) at 39.2%, worsening of cardiac disorders at 8.0%, worsening of unknown conditions leading to death at 6.5%, worsening of non-cardiac disorders at 5.1%, atrial fibrillation at 5.0%, and transplant at 3.0%. The registry does not state the denominator or detailed coding rules for these percentages, so they should be read as posted rather than used to derive additional counts.

Death counts by arm are not reported in the registry record. The record does not provide enough detail to infer event timing, severity grading rules, relatedness to the device or treatment strategy, or whether participants could contribute more than one event term. These summaries describe reported adverse-event data; they do not, by themselves, establish a causal comparison.

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

The posted results describe similar primary composite event counts in the two randomized arms: 43.0 in the Device Managed Arm and 44.0 in the Traditional Arm. The unadjusted risk-difference estimate is close to zero, and its confidence interval crosses zero. The sponsor-reported hazard ratio is also close to its null value, with a confidence interval that crosses one. Together, these summaries do not isolate a clear direction of difference on the composite endpoint.

This does not establish that the treatment strategies are equivalent or that no difference exists. The intervals allow effects in either direction, and the registry does not report an equivalence or non-inferiority design. The unadjusted p-value of 0.861 should not be read as proof of no effect. Instead, it indicates that the observed data are not unusual under the tested null comparison, subject to the assumptions of the re-calculation.

The endpoint combines cardiac-related unplanned admissions, cardiovascular death, and progression to chronic atrial fibrillation. Without component-specific results, the posted composite comparison cannot identify whether the components followed the same pattern or whether one component contributed more to the overall result. It also cannot be generalized automatically to other outcomes or populations not described by the registry.

The study was randomized and parallel, but it was unmasked. The registry record does not describe the randomization process, analysis population, missing-data handling, detailed endpoint definitions, or sponsor model. Those omissions limit assessment of potential bias and the reproducibility of the reported analysis. The serious adverse-event counts are descriptive and are not a substitute for the primary efficacy comparison.

In general, a clinical trial result should be interpreted in light of its design, endpoint definitions, analysis plan, effect estimates, and uncertainty. The available record supports a description of the posted counts and estimates, but not a definitive claim about treatment benefit, lack of benefit, or equivalence. No medical advice follows from these statistical summaries.

17. Why This Trial Matters Statistically

This trial illustrates why a clinical comparison should not be reduced to the event counts alone. The primary endpoint is a composite, and a similar overall count can conceal different patterns among its components. Component results would help show whether admissions, cardiovascular deaths, and progression to chronic atrial fibrillation contributed similarly, but those results are not reported in the registry record.

It also demonstrates the value of distinguishing estimands and effect measures. The unadjusted re-calculation compares observed group risks on an absolute scale; the sponsor reports a hazard ratio that summarizes a time-to-event contrast. These measures have different interpretations and null values. Presenting both with their uncertainty helps prevent readers from treating a single point estimate as the whole result.

The estimates are close to their null values, but both confidence intervals extend across them. That combination is a useful reminder that a non-small p-value is not proof of equivalence, and that precision depends on the full range of plausible values rather than the point estimate alone. The missing original design assumptions also mean that the planning illustrations cannot be mistaken for the trial’s actual design rationale.

Finally, the record shows how incomplete reporting affects statistical interpretation. Missing details about analysis populations, missing data, model specification, and multiplicity limit the ability to reproduce or fully evaluate the findings. Transparent reporting of these items allows readers to separate what the observed data show from what remains uncertain.

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 available record. The endpoint is a composite, but the registry does not report results for its individual components. It is therefore not possible to determine the component-specific event patterns or to see whether the overall comparison is driven by one component. Definitions and adjudication procedures for the component outcomes are also not reported in the registry record.

The outcome group denominators are 199.0 and 197.0, while enrollment is recorded as 420. The registry record does not explain participant flow, exclusions, missing outcome data, or the analysis population. The reported result cannot be assumed to include all randomized participants under an intention-to-treat approach because that approach is not specified. Follow-up completeness and censoring details are not reported.

The sponsor’s hazard-ratio analysis is presented without a method description or p-value. The registry does not identify the model, covariates, censoring rules, or analysis population. The re-calculation is unadjusted and uses posted summary counts; it cannot reproduce a time-to-event model. The absence of a flagged discrepancy does not resolve the difference in statistical approaches.

The trial is listed as randomized and unmasked, but randomization procedures and allocation concealment are not described. The registry record does not report the original sample-size justification, target effect, interim analyses, or a statistical analysis plan. It also does not report a multiplicity strategy. These omissions constrain assessment of prespecification and potential analytic flexibility.

Safety reporting is limited to arm-level adverse-event summaries and listed terms. The record does not report death counts by arm, event timing, relatedness assessments, or sufficient coding detail to interpret the percentages’ denominators. The available summaries should therefore be treated as descriptive registry results rather than a complete account of safety analyses.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: TReatment of Atrial Fibrillation With Dual dEfibrillator in Heart Failure Patients — NCT00345592.
• Registry record last updated 2017-03-28; status last verified 2017-02.
• Results first posted 2014-06-11.
• 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

NCT00345592 is a completed, randomized, unmasked, parallel Phase 4 trial sponsored by Boston Scientific Corporation. It compared automatic device-managed therapy for atrial arrhythmias with physician-commanded therapy in a hospital environment among patients with congestive heart failure and an indication for CRT defibrillator implantation. Registry enrollment is 420.

The primary composite outcome was unplanned hospital admissions for cardiac reasons, death of cardiovascular causes, or progression to chronic atrial fibrillation over 3 years from randomization (39 months total). The outcome counts were 43.0 in the Device Managed Arm and 44.0 in the Traditional Arm. The sponsor-reported hazard ratio was 0.987, with a 95% confidence interval from 0.684 to 1.503. The unadjusted re-calculation reports a risk difference of 0.007, with a 95% confidence interval from -0.074 to 0.089 and an unadjusted p-value of 0.861.

Secondary outcomes, analysis populations, missing-data methods, detailed model specifications, and the original sample-size justification are not reported in the registry record. The posted estimates should be interpreted with their uncertainty and these reporting limitations in view.