STOP AF First: Cryoballoon Catheter Ablation in an Antiarrhythmic Drug Naive Paroxysmal Atrial Fibrillation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for STOP AF First: Cryoballoon Catheter Ablation in an Antiarrhythmic Drug Naive Paroxysmal Atrial Fibrillation (NCT03118518), a randomized na study. The primary outcome is Percentage of Participants With Treatment Success at 12 Months After Antiarrhythmic Drug (AAD) Initiation or Ablation Utilizing the Arctic Front Advance™ Cardiac CryoAblation Catheter..

2. Clinical Question

This is a comparison of two treatment strategies in a randomized, parallel-group trial. Its primary measure is a binary outcome: each participant is classified according to whether treatment success was achieved by the specified follow-up. The registry record presents group percentages and a between-group risk-difference estimate with a confidence interval and an unadjusted p-value.

The outcome does not capture only rhythm monitoring. Success is defined as the absence of a set of treatment-failure events, including specified documented arrhythmia, subsequent left-atrial surgery or ablation, and certain subsequent cardioversions. The definition also includes acute procedural failure for the ablation arm and later use of specified antiarrhythmic drugs for that arm. Those elements make the endpoint a composite of clinical events and treatment-related events, rather than a single measure of arrhythmia alone.

The registry record identifies quality-of-life scores at baseline compared with 12 months and healthcare utilization as secondary outcomes. Detailed results for those outcomes are not reported in the registry record. The primary comparison therefore addresses the posted treatment-success outcome, not every aspect of health status or resource use.

3. Trial Design

STOP AF First is recorded as a randomized, open-label, parallel-group trial. Randomization assigns participants to a treatment strategy, while the parallel design keeps the assigned groups separate during follow-up. Masking is listed as none, so the record does not describe the study as blinded.

The registry record lists enrollment as 225. The primary outcome population is described as subjects who received the treatment they were randomized to, a modified intent-to-treat population. The posted primary outcome groups are 104 subjects treated with cryoballoon catheter ablation as randomized and 99 subjects treated with antiarrhythmic drug initiation. These are the denominators shown for the primary outcome; the record does not explain in detail how people who did not receive their assigned treatment or who lacked outcome data were handled.

The trial began on 2017-06-23, and the primary completion date is 2020-06-25. Its status is completed. The phase is listed as NA. The sponsor is Medtronic Cardiac Ablation Solutions.

The primary outcome timeframe is randomization to 12 months. The endpoint compares treatment success following AAD initiation in the control arm with success following pulmonary vein isolation using the cryoablation catheter in the treatment arm. Because masking is listed as none, participants and study personnel were not described as blinded in the record. The registry record does not report whether outcome assessors were masked, nor does it describe procedures intended to limit the effect of open-label treatment knowledge on event assessment.

The brief study summary describes the aim as providing data on the safety and effectiveness of the catheter for recurrent symptomatic paroxysmal atrial fibrillation without requiring subjects to be drug refractory. That is the stated study aim, not a substitute for the specific endpoint definition or statistical comparison. The registry record does not report the trial's original sample-size justification or its detailed statistical analysis plan.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Of 225 enrolled participants, 210 met inclusion criteria and were randomized to treatment. Of the 15 who exited prior to randomization: 11 did not meet inclusion/exclusion criteria, 2 withdrew, 1 was lost to follow-up and 1 had study enrollment close prior to randomization.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Subjects who were received the treatment they were randomized to (modified intent to treat).

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 Percentage of Participants With Treatment Success at 12 Months After Antiarrhythmic Drug (AAD) Initiation or Ablation Utilizing the Arctic Front Advance™ Cardiac CryoAblation Catheter., measured over Randomization to 12 months.

The primary endpoint is the percentage of participants with treatment success from randomization to 12 months. Success is defined as the opposite of treatment failure. The registry record lists failure events that include acute procedural failure in the ablation arm; documented AF, AT, or AFL on monitoring or ECG after the specified post-treatment period; subsequent AF surgery or left-atrial ablation; and later cardioversion after the specified period. The definition also counts Class I or III antiarrhythmic drug or sotalol use after the blanking period in the treatment arm.

This binary endpoint combines several ways that the assigned strategy might fail to meet the trial's success definition. A participant either meets the composite definition of success or does not. The measure is useful for comparing the overall proportion meeting that prespecified clinical-trial outcome, but it does not show which individual failure component drove the result. Component-specific event results are not reported in the registry record.

The arm-specific definitions are not identical: acute procedural failure and later use of specified antiarrhythmic drugs are treatment-arm-only components, while the post-treatment intervals are described in relation to ablation or AAD optimization. Those features matter when interpreting a between-group contrast. The outcome should be understood as treatment success under the registry's composite rules, not as an isolated measure of arrhythmia burden, quality of life, or healthcare use.

For binary outcomes, a percentage communicates how often the defined event occurred within the analyzed group. It does not by itself explain the precision of the estimate or establish what caused the difference between groups. The confidence intervals and comparison provide additional statistical context.

7. Results Posted in the Registry

• Subjects Treated With Antiarrhythmic Drug Initiation: 45.5% (45/99) versus 74.0% (77/104) on control; risk difference -28.6 percentage points (95% CI -41.5 to -15.7), risk ratio 0.61 (0.48–0.78); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary because each participant is classified as meeting or not meeting the composite treatment-success definition. The registry reports the percentage meeting success in each group. For a binary outcome, the group percentage is an estimate of the event probability in that group. Its uncertainty depends in part on the number of observations and the observed proportion. A confidence interval expresses this sampling uncertainty using a method that also depends on the statistical procedure.

What does the risk difference represent?

The risk difference subtracts one group's event probability from the other's, with the comparison direction determining the sign. In this registry comparison, antiarrhythmic drug initiation is contrasted with cryoablation. The posted risk-difference estimate is negative, consistent with the lower success percentage in the antiarrhythmic-drug group. A value of zero would correspond to equal estimated event probabilities under that comparison. The interval for the risk difference is entirely below zero. This is a direct reading of the posted comparison, not a new calculation.

A risk difference is expressed on the probability scale and describes an absolute contrast between groups. It differs from a risk ratio, which compares probabilities by division, and an odds ratio, which compares odds. The registry also posts risk-ratio and odds-ratio estimates, but those measures answer different questions and should not be treated as interchangeable with the risk difference. Because the primary interpretation can be made from the group percentages and the risk-difference comparison, alternate measures need not be used to restate the result.

How should the confidence intervals be read?

A confidence interval is a range calculated from the observed data using a statistical method. In general, it describes the uncertainty associated with an estimate under that method and its assumptions. It is not a range containing a fixed proportion of individual participant outcomes, and it does not mean that every value inside the range is equally plausible. The registry reports 95% confidence intervals for the arm-specific percentages and for the between-group risk difference. These are separate intervals for separate quantities.

The arm-specific intervals describe uncertainty in each percentage. The risk-difference interval directly describes uncertainty in the contrast. The latter is the relevant interval for judging which directions and magnitudes of the between-group contrast are compatible with the analysis. Since it lies below zero, its direction agrees with the posted percentages. An interval can be statistically informative while still allowing uncertainty about the precise magnitude of a contrast.

What does the p-value add?

The unadjusted p-value is reported as <0.001. In general, a p-value measures 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, and it does not quantify the chance that the result occurred by chance in an everyday sense. It also does not describe the size or clinical importance of the difference. The confidence interval and the observed percentages are needed to understand direction and precision.

The registry calls the p-value unadjusted. The record does not report whether a multiplicity procedure was used for the primary result or for the wider set of outcomes. Without such information, the posted p-value should be described as reported, not assumed to account for multiple testing.

Why does the endpoint definition matter?

The endpoint's composite structure means that several different events can prevent a participant from being classified as successful. A composite can provide an overall outcome for comparison, but its interpretation depends on which components are included and how they are defined. Here, some criteria are specific to one treatment arm, and the timing references differ for ablation and drug optimization. The registry record does not report component-level outcome counts, so the contribution of each event type to the overall percentage cannot be assessed from the posted primary result.

As a general statistical matter, outcome ascertainment can affect a binary comparison when classification depends on monitoring, clinical decisions, or treatment changes. The trial is listed as unmasked. The record does not say whether outcome assessment was independently adjudicated or whether assessors were blinded, so those safeguards cannot be assumed.

What does the analysis population imply?

The primary population is described as participants who received their randomized treatment, labeled modified intent to treat. This defines the group represented by the posted primary outcome. It is not identical by definition to an analysis that retains everyone according to randomized assignment regardless of treatment received. The registry record does not give further details on deviations, exclusions, or missing outcome handling, so the consequences of those decisions cannot be evaluated.

The comparison can therefore be read as the posted group-level result for the stated population and endpoint. It should not be expanded into claims about other analysis populations, individual failure mechanisms, or outcomes that the registry does not report.

10. Confidence Intervals and Precision

The registry reports 95% confidence intervals for both group percentages. The cryoablation success estimate is 73.7%, with an interval from 64.0% to 81.2%. The antiarrhythmic-drug success estimate is 45.0%, with an interval from 34.6% to 54.7%. These intervals show that the underlying group percentages are not known with exact precision; the point estimates are the best single summaries in the posted results, while the ranges convey uncertainty under the analysis method.

The between-group risk difference has its own confidence interval, which lies below zero. That interval is more directly useful for assessing uncertainty in the contrast than comparing the endpoints of the two separate arm-specific intervals. The registry's unadjusted p-value is <0.001, but a p-value does not show the range of plausible effect sizes. The confidence interval supplies that different kind of information.

Precision is not the same as validity or importance. A narrow interval would indicate less sampling uncertainty under the method, but would not resolve limitations in the endpoint definition, outcome ascertainment, or analysis population. Conversely, an interval that includes a broad range of effects would leave more uncertainty about magnitude. The posted intervals should be interpreted in conjunction with the open-label design and composite endpoint.

The interval calculations rely on statistical assumptions. The registry record does not report the methods used to calculate the primary confidence intervals, so details such as the exact interval procedure cannot be assessed. The displayed precision also does not address possible bias from missing outcomes or other design and analysis choices. Those details are not reported in the registry record.

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 sample-size illustration is a planning aid based on the observed treatment-success effect, not a report of the trial's original design assumptions. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row considers an effect equal to a stated fraction of the observed effect. The figures are participants per arm, not total participants or total events.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the selected effect at the stated significance level, if the assumptions hold. The 90% power column gives the corresponding planning number for a 90% chance. These are prospective design calculations: they describe hypothetical study planning, not what happened in the completed trial. They are not observed power.

The rows consider planning for 100%, 75%, and 50% of the observed effect. For the 100% row, the illustration gives 46 participants per arm for 80% power and 60 for 90% power. For 75% of the observed effect, it gives 79 participants per arm for 80% power and 105 for 90% power. For 50% of the observed effect, it gives 170 participants per arm for 80% power and 226 for 90% power. Smaller effects require more participants under these assumptions because they are harder to distinguish from random variation.

The sample-size curve is a visual representation of the same planning relationship: as the effect being targeted becomes smaller, the required group size increases. These calculations use the observed effect as their reference, so they should not be read as evidence that the original trial was designed with these assumptions or achieved a particular level of power. The registry record does not report the original sample-size justification or original design assumptions.

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 = 0.740; treatment proportion p₁ = 0.455; average p̄ = 0.597.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6935 = 1.3593.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6634 = 0.5584.
4. n = (1.3593 + 0.5584)² / (-0.2858)² = 45.0, rounded up to 46 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 <- 0.740384615384615                          # control proportion
p1 <- 0.454545454545455                          # 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(3118518)
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 = 46 (80% power), 60 (90% power)
 75% of observed effect: n per arm = 79 (80% power), 105 (90% power)
 50% of observed effect: n per arm = 170 (80% power), 226 (90% power)
power.prop.test: 45 
Simulated power at n = 46 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. Multiplicity, Missing Data and Analysis Populations

The primary outcome population is described as modified intent to treat: subjects who received the treatment to which they were randomized. This makes the analysis population explicit at a broad level, but the registry record does not report a detailed account of exclusions, treatment crossovers, protocol deviations, or how participants without an observed 12-month outcome were handled. Missing-data methods, if any, are not reported in the registry record.

This matters because the posted percentages are interpreted for the analyzed population and depend on outcome classification. In general, if outcomes are missing, the way missing observations are treated can affect both the estimated group percentages and their uncertainty. Without the number of missing outcomes and the handling method, it is not possible to assess whether missingness could have changed the comparison. No missing-data mechanism should be assumed.

The registry record lists two secondary outcomes: quality-of-life scores at baseline compared with 12 months, and healthcare utilization. Detailed secondary outcome results are not reported in the registry record. The record does not report a multiplicity adjustment or a hierarchy describing how the primary and secondary outcomes were to be interpreted together. The p-value for the primary comparison is explicitly unadjusted. It should not be described as adjusted for testing multiple outcomes unless the record says so.

There are four outcome measures listed, while zero analyses are listed in the record's analysis count. That listing does not supply a statistical plan or explain how the posted primary comparison was derived. The registry record does not report the planned analysis model, covariate adjustment, interim analyses, or a prespecified strategy for handling multiple comparisons. These items cannot be inferred from the posted result.

Randomization supports a comparison of assigned strategies, but the primary endpoint population is defined by receipt of randomized treatment rather than by an explicitly described all-randomized analysis. The record does not report a separate intention-to-treat analysis. It is therefore important to keep conclusions tied to the stated modified intent-to-treat population and not assume that all randomized participants were included in the primary comparison.

14. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: syncope (2.0%), atrial fibrillation (1.9%), osteoarthritis (1.9%), angina unstable (1.0%), bradycardia (1.0%).

The serious adverse event figures are reported for 104 participants randomized and treated with cryoablation and 99 randomized and treated with antiarrhythmic drugs. The registry records 16 affected by serious adverse events in the cryoablation group and 14 in the antiarrhythmic-drug group. The other adverse-event counts are 8 and 16, respectively. Deaths are reported as 0 in each group.

These counts describe the registry's recorded safety figures for the stated groups. They should not be confused with the primary treatment-success outcome, which has a different definition and analysis. The record also lists serious adverse event terms and their percentages, including Syncope at 2.0%, Atrial fibrillation at 1.9%, and Osteoarthritis at 1.9%. Other listed terms are Angina unstable at 1.0%, Bradycardia at 1.0%, and Palpitations at 1.0%.

Counts alone do not establish that an event was caused by treatment, and they do not describe severity, duration, or clinical course beyond the registry's classification. The record does not report further detail about event timing, recurrence, or attribution. These figures are descriptive safety data, not a complete characterization of comparative safety.

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

The posted results show a higher treatment-success percentage for cryoablation than for antiarrhythmic drug initiation under the trial's 12-month composite definition. The comparison estimate is oriented as drug initiation relative to cryoablation, its confidence interval lies below zero, and its unadjusted p-value is <0.001. The group percentages and comparison together describe the observed difference and its statistical uncertainty in the stated analysis population.

The result does not mean that every participant in one group succeeded or every participant in the other group failed. It does not identify which part of the composite endpoint accounts for the contrast, because component-specific results are not reported in the registry record. It also does not directly establish a difference in quality of life or healthcare utilization; although those outcomes are listed as secondary outcomes, their detailed results are not reported in the registry record.

The endpoint includes a mixture of rhythm findings, procedures, cardioversions, and treatment-use criteria, with some elements applying only to the ablation arm. Therefore, the comparison concerns success as defined by these rules rather than a single uniform biological measure. The 12-month timeframe also limits the result to the follow-up period specified for the primary outcome; longer-term results are not reported in the registry record.

The trial is randomized but unmasked. The registry record does not report whether outcome assessors were masked, whether events were independently adjudicated, or how missing data were handled. Those unreported details affect how fully the robustness of the comparison can be evaluated. The stated modified intent-to-treat population should also be kept in view when considering who is represented by the primary result.

Statistical significance does not by itself establish clinical importance, and the confidence interval does not eliminate uncertainty. The posted result is evidence about this particular trial population, treatment comparison, endpoint definition, and follow-up. It should not be generalized beyond those boundaries without additional evidence.

16. Why This Trial Matters Statistically

The statistical interest of STOP AF First lies in the way its result combines randomization, a binary outcome, and a clinically structured composite endpoint. Random allocation is intended to support a fair comparison of the assigned strategies, while the group percentages communicate the frequency of meeting the endpoint. The risk difference then expresses the contrast on an absolute probability scale, with a confidence interval showing uncertainty around that contrast.

Interpreting the estimate requires attention to the endpoint's construction. Treatment success is not a single event; it is the absence of several kinds of treatment failure. Some criteria apply only to the ablation arm, and the timing rules are framed around ablation blanking or drug optimization. This illustrates why a statistically clear overall contrast can still leave important questions about the contributing outcome components.

The trial also demonstrates the distinction between a reported result and a planning calculation. The sample-size illustration uses fractions of the observed effect under stated assumptions. It can help show how anticipated effect size influences planning, but it cannot reconstruct the original design rationale or indicate the trial's observed power. Those original design assumptions are not reported in the registry record.

Finally, design and reporting details shape the limits of interpretation. The trial is open-label, the primary population is described as modified intent to treat, and the registry record does not report missing-data handling, a multiplicity plan, or component-level results. These are not reasons to disregard the posted comparison; they identify which statistical questions remain unanswered. A careful reading can recognize the direction and precision of the primary result while keeping its scope tied to the endpoint, population, and available reporting.

17. 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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations are specific to the information reported for this trial. First, masking is listed as none. The registry record does not state whether outcome assessors were masked or whether an independent committee adjudicated outcome events. Because the endpoint includes monitoring findings and treatment-related decisions, the absence of reported assessment procedures leaves uncertainty about how classification was protected from knowledge of treatment assignment.

Second, the primary endpoint is a composite whose criteria are not identical across arms. Acute procedural failure and later use of specified antiarrhythmic drugs are treatment-arm-only criteria, and the post-treatment periods are described differently for ablation and AAD optimization. The registry record does not report component-level success or failure results, so the relative contribution of the individual criteria cannot be examined.

Third, the primary population is subjects who received the randomized treatment. The record does not report detailed exclusions, crossover handling, missing outcome counts, or missing-data methods. It is therefore not possible to assess how the result might compare with an all-randomized analysis or how missing outcomes may have influenced the estimates.

Fourth, the registry record does not report the original sample-size justification, the detailed statistical analysis plan, interim analyses, or a multiplicity strategy. It lists quality-of-life scores and healthcare utilization as secondary outcomes, but detailed results for those outcomes are not reported in the registry record. The primary result consequently cannot answer questions about those outcomes or about a broader family of prespecified comparisons.

Finally, the primary follow-up timeframe is randomization to 12 months. Results beyond that timeframe are not reported in the registry record. These limitations define the boundaries of what can be inferred from the posted outcome and do not replace the observed group percentages and comparison.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: STOP AF First: Cryoballoon Catheter Ablation in an Antiarrhythmic Drug Naive Paroxysmal Atrial Fibrillation — NCT03118518.
• Registry record last updated 2025-02-13; status last verified 2025-02.
• Results first posted 2021-08-11.
• 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.

21. Record Summary

STOP AF First is a completed, randomized, open-label, parallel-group trial comparing cryoballoon catheter ablation with antiarrhythmic drug initiation for recurrent symptomatic paroxysmal atrial fibrillation in people described as antiarrhythmic-drug naive. The primary outcome is the percentage with treatment success from randomization to 12 months, analyzed among subjects who received their randomized treatment.

The posted success percentages are 73.7% for cryoablation and 45.0% for antiarrhythmic drug initiation. The comparison favors a higher observed success proportion in the cryoablation group under the registry's composite definition, with a 95% confidence interval for the risk difference lying below zero and an unadjusted p-value of <0.001.

The endpoint combines several failure criteria, some specific to one arm. Detailed component results, secondary outcome results, missing-data methods, the original sample-size justification, and the detailed statistical plan are not reported in the registry record. The findings should be interpreted within the stated population, endpoint, and follow-up period.