Clinical Trial Comparing Devices Used for Cardioversion of Atrial Fibrillation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Trial Comparing Devices Used for Cardioversion of Atrial Fibrillation (NCT05992623), a randomized na study. The primary outcome is The Number of Participants in Normal Sinus Rhythm (NSR) by ECG After the First DCCV Shock.

2. Clinical Question

3. Trial Design

The registry describes a pragmatic, randomized, open-label, prospective trial conducted at a single center. Its model is crossover: the initial comparison is between the Zoll RBW and Lifepak BTE approaches, and participants without success after the second full-output shock could receive shocks using the alternative waveform. Crossover participants could receive up to 2 full-output shocks, with a minimum of 1 minute between shocks, according to the arm descriptions. The trial is recorded as completed, with enrollment of 546.

The device strategies differ in both waveform and energy setting: 200J RBW with Zoll and 360J BTE with Lifepak. The primary outcome is the count of participants in normal sinus rhythm by ECG after the first shock, assessed at least 1 minute after delivery. A secondary outcome considers NSR after the first or second shock. Another secondary outcome concerns NSR after crossover from the alternative defibrillator. These outcomes address different stages of the treatment sequence and should not be read as interchangeable estimates of the initial-shock comparison.

Random allocation is recorded, but the method used to generate or conceal the allocation is not reported in the registry record. Masking is recorded as none, so participants and clinical personnel were not masked according to the registry. Further protocol details, including whether the analysis followed intention-to-treat principles, how deviations from the assigned device strategy were handled, and the original sample-size justification, are not reported in the registry record. The record lists a total enrollment, while the primary results are presented by arm.

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

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 The Number of Participants in Normal Sinus Rhythm (NSR) by ECG After the First DCCV Shock, measured over At least 1 minute after shock delivery.

The primary endpoint counts participants whose ECG showed normal sinus rhythm after the first direct-current cardioversion shock. The registry specifies that the rhythm assessment occurs at least 1 minute after shock delivery. It compares a single full-output 200J RBW shock from the Zoll Series R defibrillator with a single full-output 360J BTE shock from the Lifepak 15 defibrillator.

This endpoint is a binary outcome at the participant level: each participant either met the recorded ECG criterion or did not. Counting participants with NSR gives an interpretable measure of how often the specified rhythm was observed following the initial shock. The timing matters: it focuses on the immediate response after shock delivery, rather than rhythm status over a longer follow-up period. The registry does not report a longer-term rhythm endpoint in the primary outcome description.

The primary result is not a pure comparison of waveform alone. The two strategies use different devices, waveform types, and energy settings, so the observed comparison pertains to the overall device-and-shock strategies as recorded. The endpoint also does not itself describe adverse events, subsequent shocks, or outcomes after crossover. Those are addressed separately in the registry’s secondary outcomes and safety records. Details of ECG adjudication, including whether interpretation was blinded or independently reviewed, are not reported in the registry record.

7. Results Posted in the Registry

• 360J Synchronized Biphasic Truncated Exponential Waveform (BTE) Shock From Lifepak 15 Defibrillator: 84.4% (233/276) versus 82.6% (223/270) on control; risk difference 1.8 percentage points (95% CI -4.4 to 8.1), risk ratio 1.02 (0.95–1.10); unadjusted two-proportion z-test p = 0.565.

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.

The Number of Participants in Normal Sinus Rhythm (NSR) by ECG After the First or Second DCCV Shock

• 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:
  • 360J Synchronized Biphasic Truncated Exponential Waveform (BTE) Shock From Lifepak 15 Defibrillator: 89.9% (248/276) versus 91.1% (246/270) on control; risk difference -1.3 percentage points (95% CI -6.2 to 3.7), risk ratio 0.99 (0.93–1.04); unadjusted two-proportion z-test p = 0.617.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 360J Synchronized Biphasic Truncated Exponential Waveform (BTE) Shock From Lifepak 15 Defibrillator and the control. The interval gives the range of effects that remain compatible with the data.

The Frequency of NSR One Minute After the First or Second Full Output DCCV Shock is Delivered by a Zoll Series R RBW Waveform Defibrillator and a Lifepak Series 15/20 BTE Waveform Defibrillator After Crossing Over From the Alternative Defibrillator.

• 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:
  • Crossed Over to 360J Synchronized Biphasic Truncated Exponential Waveform (BTE) Shock From Lifepak15: 54.5% (12/22) versus 25.0% (6/24) on control; risk difference 29.5 percentage points (95% CI 2.5 to 56.6), risk ratio 2.18 (0.99–4.81); unadjusted two-proportion z-test p = 0.040.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Crossed Over to 360J Synchronized Biphasic Truncated Exponential Waveform (BTE) Shock From Lifepak15 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the question beyond the first shock. One measures NSR after the first or second shock, while another concerns NSR after crossover to the alternative waveform. Taken together, they describe later points in the cardioversion sequence rather than an independent replication of the primary endpoint. The broader first-or-second-shock outcome is consistent with asking about response across more than the initial shock, while the crossover outcome focuses on participants who did not succeed with the initial device sequence.

The overall pattern does not change the central reading of the primary comparison: the initial-shock result does not show clear evidence of a difference between the device strategies. A secondary signal in the crossover analysis is not directly comparable to that primary result because crossover follows unsuccessful shocks and selects a subgroup based on the earlier response. It therefore cannot be interpreted as if the original randomized groups had simply been reassigned for a new head-to-head comparison.

Secondary results generally carry less weight when they are not the primary question, especially when several outcomes or analyses are examined. The registry records 3 outcome measures and 3 analyses, but it does not report a multiplicity procedure or a prespecified hierarchy for secondary testing. Without such information, a nominal p-value for a secondary endpoint has a greater risk of being a chance finding among the set of analyses. This does not make the secondary observations irrelevant; it means they are better viewed as supporting or hypothesis-generating evidence rather than definitive proof.

The record does not report whether each secondary analysis was prespecified in a detailed analysis plan or how missing observations were treated. The results should therefore be interpreted according to their stated endpoint and population, with the crossover analysis kept distinct from outcomes in the initial randomized arms. No single secondary result should be used to claim a general treatment advantage beyond the population and treatment stage it describes.

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

• The Number of Participants in Normal Sinus Rhythm (NSR) by ECG After the First or Second DCCV Shock
• The Frequency of NSR One Minute After the First or Second Full Output DCCV Shock is Delivered by a Zoll Series R RBW Waveform Defibrillator and a Lifepak Series 15/20 BTE Waveform Defibrillator After Crossing Over From the Alternative Defibrillator.

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a Chi-squared analysis for the primary superiority comparison. The posted recalculation also presents an unadjusted risk difference and interval based on the arm-level counts. These methods answer related but distinct questions: the test summarizes evidence against a null comparison, while the risk difference expresses the estimated absolute contrast between the observed proportions. The contrast is defined as the Lifepak proportion minus the Zoll proportion, so a positive value points toward a higher observed proportion in the Lifepak arm.

What does the risk difference express?

A risk difference is the difference between the proportions experiencing an outcome in two groups. Here, the event is NSR by ECG after the first shock. The estimated risk difference is 0.018. This is an absolute contrast on the proportion scale, not a relative measure. It is distinct from a risk ratio or odds ratio, which express comparisons on relative scales. The registry also posts relative measures, but the absolute difference is often straightforward to interpret because it directly describes the gap between the observed group proportions.

The risk difference is unadjusted: it uses the reported group counts and does not account for other participant characteristics or covariates. The registry does not report an adjusted primary estimate. Randomization is intended to support comparability of groups, but the way allocation was generated, allocation concealment, baseline balance, and analysis population are not reported in the registry record. Thus, the posted comparison should be interpreted as the stated unadjusted arm-level analysis, not as a covariate-adjusted estimate.

How should the p-value be read?

The primary reported p-value is 0.565 from a Chi-squared analysis. A p-value describes how unusual the observed data, or data more extreme, would be under a specified null model and the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. A relatively large p-value does not prove equivalence or demonstrate that the strategies have identical outcomes. The registry does not report an equivalence or non-inferiority framework, including a margin that would define an acceptable difference.

The Chi-squared test compares categorical outcomes across groups. Its use is consistent with a binary endpoint recorded as counts of participants with and without NSR. The registry does not report additional details about the test implementation, such as continuity correction or the exact handling of any missing endpoint values. The recalculation is described as simple and unadjusted; it is not a substitute for details of the sponsor’s full analysis plan.

Why do intervals matter?

An interval around an estimate conveys uncertainty in the estimated contrast. The primary risk-difference interval extends from -0.044 to 0.081. Since it includes zero, the data are compatible with no difference under the interval procedure, as well as with differences in either direction. An interval is not a range in which the true effect is guaranteed to lie. Its interpretation depends on its construction and confidence level; the confidence level is not reported in the registry record for this recalculated interval.

Intervals can also help distinguish an imprecise estimate from a precise estimate near zero. The primary result has an interval that spans negative and positive values, so the point estimate alone should not be treated as a definitive directional finding. The data do not rule out a meaningful contrast merely because the p-value is not small; what counts as meaningful must be defined clinically, and a threshold is not reported in the registry record.

What does crossover change?

The crossover design permits a different device waveform to be used after unsuccessful shocks with the initially used device. This provides information about outcomes after a treatment sequence, but it changes the composition of the groups being compared. Participants who cross over have already experienced an unsuccessful response to the initial strategy. Comparisons among crossover groups therefore do not retain the same interpretation as the randomized initial comparison. They are not a fresh randomized assignment of the alternative devices among all participants.

For the crossover outcome, the registry reports a Chi-squared p-value of <0.05 and the recalculation reports an unadjusted p-value of 0.04. That result is a secondary comparison in a selected subset and is not adjusted for multiple outcome analyses. It should be read as a signal in the crossover data, not as confirmation of a general advantage for one device strategy in the full randomized population.

The registry does not report the original statistical analysis plan, planned handling of missing data, or a detailed definition of analysis populations. Those omissions limit assessment of whether all posted analyses were planned in advance and whether the analysis followed the intended randomized allocation. General statistical interpretation must therefore remain tied to the endpoints, counts, and comparisons actually recorded.

11. Confidence Intervals and Precision

For the primary comparison, the recalculated risk difference is 0.018, with an interval from -0.044 to 0.081. The interval crosses zero, so the data do not distinguish a positive contrast from no contrast or a negative contrast at the level represented by that interval. It is wider than a narrow interval tightly concentrated around the point estimate would be, which reflects uncertainty in the estimated difference. The confidence level for this recalculated interval is not reported in the registry record.

The interval is useful because it shows more than the direction of the point estimate. The point estimate favors Lifepak numerically, but the interval includes values on both sides of zero. Therefore, the results are compatible with a range of possible contrasts, rather than only the point estimate. The registry’s p-value of 0.565 is consistent with the absence of strong evidence against the null comparison, but it should not be interpreted as proof that the strategies are equivalent.

Precision depends on the observed counts, outcome frequency, and analysis method. The primary group counts are 270 and 276, and the numbers with NSR after the first shock are 223 and 233. These data yield an estimate with uncertainty; they do not establish that any particular small difference has been excluded. A clinically meaningful threshold is not reported in the registry record, so the interval cannot be judged against a stated threshold for importance.

Precision also differs across endpoints. The crossover comparison involves a smaller, selected group than the initial randomized comparison, so its estimate should be read in light of that limited information and its different design context. The registry does not report confidence intervals for the sponsor’s analyses, and the confidence level of the posted recalculated intervals is not specified. Interpretations should therefore identify which estimate and interval are being discussed and avoid treating a secondary, unadjusted finding as more precise or more conclusive than the record supports.

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 are illustrations based on the observed effect, not the trial’s original enrollment rationale. The figures for these non-time-to-event outcomes are participants per arm, not totals across arms and not total events. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set at the stated fraction of the observed effect.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect and the calculation assumptions were correct. The 90% power column describes the corresponding planning target for a greater chance of detecting the same specified effect. These are prospective design quantities, not measures of the trial’s observed power.

Rows based on 100%, 75%, and 50% of the observed effect ask how the planning requirement changes when the target effect is reduced. The smaller the effect one aims to detect, the more participants are generally needed, because a smaller contrast is harder to distinguish from sampling variation. The posted figures illustrate that increase for the primary and secondary comparisons. They are not recommendations for a future study without further design work, because other assumptions, including the chosen primary endpoint and intended analysis, would also matter.

The registry’s own sample-size justification and design assumptions are not reported in the registry record. The planning calculations should not be read as evidence that the trial was designed with a particular power, nor as evidence that the observed result had a particular probability of being detected. They are hypothetical planning illustrations based on the observed estimates and the stated assumptions.

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 = 0.826; treatment proportion p₁ = 0.844; average p̄ = 0.835.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5248 = 1.0287.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5247 = 0.4416.
4. n = (1.0287 + 0.4416)² / (0.0183)² = 6,471.2, rounded up to 6,472 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 <- 0.825925925925926                          # control proportion
p1 <- 0.844202898550725                          # 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(5992623)
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 = 6,472 (80% power), 8,663 (90% power)
 75% of observed effect: n per arm = 11,633 (80% power), 15,573 (90% power)
 50% of observed effect: n per arm = 26,460 (80% power), 35,422 (90% power)
power.prop.test: 6471.2 
Simulated power at n = 6,472 per arm: 0.799 (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’s primary sponsor-reported analysis uses a Chi-squared test and gives a p-value of 0.565. The recalculated unadjusted comparison also gives a p-value of 0.565, alongside a risk-difference estimate and interval derived from the posted arm counts. The agreement between the reported p-values indicates that the displayed recalculation does not create a discrepancy with the registry’s primary test result.

The sponsor’s result is the registry’s own reported analysis and remains the direct record of the analysis method and p-value. The recalculation adds an absolute effect estimate and interval to help describe the size and precision of the comparison; it does not replace the sponsor’s test or provide details absent from the registry. The registry does not report a fuller statistical analysis plan, adjusted estimates, or the confidence level for the recalculated interval.

For the crossover secondary comparison, the registry reports a Chi-squared p-value of <0.05, while the recalculated unadjusted p-value is 0.04. These are both nominal results below the conventional 0.05 threshold as recorded, but they belong to a secondary analysis in a selected crossover group. They do not alter the interpretation of the primary comparison, and they should be considered alongside the absence of reported multiplicity adjustment and analysis-plan details.

15. Multiplicity, Missing Data and Analysis Populations

The registry records a primary endpoint and secondary outcomes, with 3 outcome measures and 3 analyses. It does not report whether the analysis plan controlled the overall chance of a false-positive finding across these comparisons. A multiplicity adjustment, testing hierarchy, or other prespecified strategy for interpreting secondary p-values is not reported in the registry record.

When several outcomes are examined, each test creates an opportunity to observe a nominally notable result by chance. This is why secondary p-values are usually interpreted with more caution than a result for a single prespecified primary endpoint. The crossover finding has particular limits because it is secondary, concerns a selected subgroup, and is presented without a reported multiplicity adjustment. Its nominal statistical signal should not be treated as confirmatory evidence of superiority for the full randomized population.

Details on missing data are also not reported in the registry record. The posted arm counts specify group sizes and outcome counts, but the record does not explain whether every randomized participant had an evaluable ECG, how any unavailable assessment was handled, or whether imputation was used. The analysis population is not described as intention-to-treat, per-protocol, or another defined population. It is therefore not possible to assess from the record whether missingness or exclusions could have affected the comparison.

Other analysis details that are not reported include the full statistical analysis plan, the original sample-size rationale, allocation concealment, and a detailed account of protocol deviations. The registry does provide the reported Chi-squared methods and p-values for the comparisons, but those entries do not answer all questions about prespecification or analysis conduct. These omissions do not negate the posted counts; they limit how completely the analysis can be evaluated and how strongly secondary findings can be interpreted.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists serious adverse events separately from other adverse events for the initial device groups and crossover groups. It records zero serious adverse events in each of the four listed groups and zero deaths in each group. The serious-event counts are therefore zero as reported, but this should be understood as the observed registry count, not proof that serious events cannot occur.

Other adverse events are recorded as counts: 127 in the initial Zoll group, 122 in the initial Lifepak group, 19 in the crossover-to-Zoll group, and 10 in the crossover-to-Lifepak group. These are not serious-event counts. The registry does not provide descriptions of the individual non-serious events in the posted safety information, and the serious-event terms list is empty.

The crossover groups represent participants who reached crossover after unsuccessful shocks, so their safety counts are not directly comparable to those in the initial randomized arms. The registry does not report a statistical comparison of adverse-event rates or details about event ascertainment and follow-up. These counts describe what the record reports; they do not support conclusions about relative safety beyond the recorded events and group definitions.

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

The primary finding is that the posted results do not establish a clear difference in NSR after the first shock between the 200J Zoll RBW and 360J Lifepak BTE strategies. The observed proportions are close, and the recalculated risk-difference interval includes zero. The result should not be translated into a claim that the strategies are identical, because the interval allows for a range of contrasts in either direction.

Nor does the result show that either strategy is definitively better. The point estimate is numerically higher for the Lifepak arm, but the p-value and interval indicate uncertainty about the direction and size of the underlying difference. The registry does not report a threshold defining what difference would be clinically important, so the posted estimate cannot be classified against a stated clinical decision boundary.

The trial compares two complete device-and-shock strategies, not waveform in isolation. The strategies differ in device, waveform, and energy setting. Any observed contrast cannot be attributed specifically to one of those features from this comparison alone. The primary outcome is an ECG assessment at least 1 minute after a single shock; it does not establish longer-term rhythm, later clinical outcomes, or effects beyond the outcome and time point recorded.

The secondary outcomes and crossover findings provide additional observations, but they answer different questions. In particular, crossover results concern participants who had not succeeded after the initial sequence and should not be generalized to all randomized participants. Because multiplicity handling and analysis populations are not reported, the secondary findings should be treated cautiously. The safety counts likewise describe events recorded in this trial and do not establish the absence of risk.

Overall, the registry supports a careful description of the observed comparison, not a broad treatment recommendation or a claim of equivalence. Interpretation should remain limited to the recorded population, device strategies, endpoint definitions, and follow-up information. Eligibility criteria, baseline characteristics, longer-term outcomes, and detailed analysis procedures are not reported in the registry record.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical comparison needs more than a count of participants with an outcome or a p-value. The primary risk difference gives the absolute direction and size of the observed contrast, while its interval communicates uncertainty. A point estimate alone can appear decisive even when the data remain compatible with effects in either direction. Reading the estimate, interval, and test result together gives a more balanced account.

The trial also demonstrates the importance of keeping endpoint timing and treatment sequence explicit. NSR after the first shock is not the same estimand as NSR after the first or second shock, and neither is equivalent to an outcome measured after crossover. The latter group is selected by the response to earlier treatment. Treating these outcomes as if they were one interchangeable comparison would obscure the design and the question each result addresses.

Device comparisons often combine several features. In this trial the devices differ in waveform and energy setting, so the randomized comparison concerns the strategies as a whole. This distinction matters when translating a statistical contrast into an explanation of what might have produced it. The posted data cannot isolate the contribution of a single component.

Finally, the record illustrates how registry reporting affects the strength of interpretation. The main counts and test result are available, but details on missing data, analysis populations, multiplicity, and the original sample-size rationale are not reported. Clear reporting of these elements helps readers assess whether findings were prespecified, how uncertainty was handled, and how much weight to give secondary analyses. Their absence calls for restraint, not speculation.

19. Limitations

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

The registry record leaves important design and analysis details unspecified. Eligibility criteria, baseline participant characteristics, allocation generation and concealment, and the handling of protocol deviations are not reported. Without these details, readers cannot fully assess the enrolled population, balance between randomized groups, or adherence to assigned strategies.

The primary comparison bundles device, waveform, and shock-energy differences. It therefore cannot identify which feature is associated with the observed contrast. The study is open label, and the registry does not report whether ECG assessment or outcome classification was blinded. Details of endpoint adjudication and missing ECG assessments are also not reported.

The record does not provide a detailed statistical analysis plan, a description of analysis populations, or a missing-data method. It also does not report an adjustment strategy for multiple outcomes. These gaps matter particularly for secondary and crossover findings, which should be interpreted as distinct from the primary randomized comparison. The crossover groups are selected after unsuccessful shocks, so their comparisons may reflect this selection as well as the subsequent device strategy.

Follow-up beyond the stated ECG assessment timing and longer-term rhythm outcomes are not described in the primary endpoint record. The registry also does not state a clinically important difference or an equivalence margin. The recalculated interval’s confidence level is not reported. Consequently, the results do not establish equivalence, long-term outcomes, or a clinically important threshold for the observed contrast.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Clinical Trial Comparing Devices Used for Cardioversion of Atrial Fibrillation — NCT05992623.
• Registry record last updated 2025-09-22; status last verified 2025-09.
• Results first posted 2025-09-22.
• 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 registry record describes a completed, single-center, investigator-initiated, open-label randomized trial with crossover, comparing 200J Zoll RBW shocks with 360J Lifepak BTE shocks for cardioversion of atrial fibrillation. Enrollment is recorded as 546. The primary endpoint is NSR by ECG at least 1 minute after the first shock.

The primary arm counts are 223 of 270 for Zoll and 233 of 276 for Lifepak. The reported Chi-squared p-value is 0.565; the recalculated unadjusted risk difference is 0.018, with an interval from -0.044 to 0.081. The posted result does not establish a clear difference between the initial strategies. Secondary and crossover outcomes add context but have distinct populations and limitations. The registry does not report the original sample-size rationale, missing-data methods, analysis populations, or multiplicity plan.