Deviating the Esophagus in Atrial Fibrillation Ablation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Deviating the Esophagus in Atrial Fibrillation Ablation (NCT01546168), a randomized na study. The primary outcome is Number of Participants With Presence of Esophageal Injury.

2. Clinical Question

The central comparison is between two approaches used during ablation: moving the esophagus with a device, or monitoring esophageal temperature without deviation. The primary endpoint concerns whether an injury was present on endoscopy, rather than a continuous measure of injury severity. The posted arm results record 5.0 participants with injury among 36.0 in the esophageal-deviation group and 4.0 among 33.0 in the temperature-monitoring group.

This question is clinically framed around a possible difference in the occurrence of endoscopically assessed injury. The registry’s description states that investigators hypothesized a reduction in injury with esophageal deviation. That statement records the study hypothesis; it is not itself evidence that the intervention reduced injuries. The numerical comparison and its uncertainty are needed to assess how the observed data relate to that question.

The study also lists procedure time, temperature, and swallowing impairment score as secondary outcomes. The registry record contains results for temperature, while details for the other listed secondary outcomes are not reported in the registry record. The primary comparison therefore addresses the injury endpoint specifically, and should not be treated as a complete account of every outcome relevant to the procedure.

3. Trial Design

The registry describes a randomized, double-blind, parallel-group trial. The listed enrollment is 88, and the study status is terminated. The study start is recorded as 2011-11 and primary completion as 2015-12. The listed phase is NA. The registry record does not give a reason for termination.

Participants were assigned to esophageal deviation or temperature monitoring. In the deviation group, an IDE device was used during AF ablation. The comparison group received luminal esophageal temperature monitoring alone, described as standard temperature monitoring. The registry labels the overall design double-blind, but further details about who was masked and how masking was maintained are not reported in the registry record.

The primary outcome was a count of participants with esophageal injury assessed by upper gastrointestinal endoscopy within 1 week of the procedure. The posted primary results list 36.0 participants in the deviation group and 33.0 in the monitoring group. The outcome description says that 17 roll-in patients and two pre-procedure withdrawals were removed from the analysis. The registry does not report additional detail about the disposition of participants or the analysis population beyond that statement.

The record lists four outcome measures and three secondary outcomes: procedure time, temperature, and swallowing impairment score. Temperature results are posted as a mean in Celsius with a standard deviation. Results for procedure time and swallowing impairment score are not reported in the registry record. No reported analyses are listed for the secondary outcomes. Details of the randomization procedure, allocation concealment, masking procedures, and the trial’s original sample-size justification are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: 88 participants were consented, but 2 withdrew prior to randomization

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 17 roll-in patients and two pre-procedure withdrawals are removed from the analysis.

5. Baseline Characteristics

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

Population: 17 roll-in patients and two pre-procedure withdrawals are removed from the analysis

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Presence of Esophageal Injury, measured over within 1 week of AF ablation procedure.

The primary endpoint counts participants with esophageal injury, as assessed by upper gastrointestinal endoscopy performed within 1 week of AF ablation. It is a binary outcome at the participant level: the registry records whether injury was present, then reports the number of participants with that finding in each group. The posted counts are 5.0 in the esophageal-deviation group and 4.0 in the temperature-monitoring group.

Endoscopy provides the specified method for identifying the endpoint. Using the same assessment window for both groups defines when the finding is sought and makes the outcome a direct comparison of observed injury presence in the registry’s stated timeframe. The endpoint does not, by itself, describe the severity, duration, or subsequent course of an injury. Those features are not included in the primary outcome definition.

The registry’s brief summary says the investigators hypothesized that esophageal deviation would reduce injury. The primary endpoint is aligned with that stated hypothesis because it captures the occurrence of injury, rather than a procedural measure such as time or temperature. However, an endpoint’s relevance to a hypothesis does not establish the result. The group counts, estimated contrast, and uncertainty must be considered together.

The analysis population is described as excluding 17 roll-in patients and two pre-procedure withdrawals. Further information about missing endoscopy assessments or how unavailable outcome data were handled is not reported in the registry record. That limits what can be concluded about completeness of endpoint ascertainment.

7. Results Posted in the Registry

• Temperature Monitoring: 12.1% (4/33) versus 13.9% (5/36) on control; risk difference -1.8 percentage points (95% CI -17.6 to 14.1), risk ratio 0.87 (0.26–2.98); unadjusted two-proportion z-test p = 0.828.

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.

Temperature

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Temperature Monitoring: mean 1.10 versus 0.26 on control; difference 0.84 (95% CI 0.59 to 1.09), standardized effect d = 1.66; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Temperature Monitoring than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes listed in the registry are procedure time, temperature, and swallowing impairment score. Of these, results are posted for temperature. Results for procedure time and swallowing impairment score are not reported in the registry record. The available secondary evidence is therefore limited to one of the three listed measures, and it does not support an overall assessment of every secondary outcome.

Temperature differs in kind from the primary endpoint. The primary question concerns whether endoscopy detected esophageal injury within 1 week; temperature is a continuous intraoperative measurement. A contrast in temperature may describe how the groups differed during the procedure, but it cannot be substituted for the injury endpoint. The primary outcome remains statistically uncertain even when a secondary measure has a more distinct statistical contrast.

Unadjusted secondary results carry less weight when several outcomes may be examined. General: Each additional statistical comparison creates another opportunity to observe a small p-value by chance, even if no underlying differences exist. A plan for controlling multiplicity can address that issue, but the registry record does not report such a plan or an adjustment. The status of temperature as a secondary outcome, the absence of reported analyses for the other listed secondary outcomes, and the lack of reported multiplicity handling all counsel against treating a single unadjusted result as decisive.

The trial lists four outcome measures overall, but the registry record does not provide full results for every listed secondary outcome. This creates a further interpretive limitation: the available results do not show whether the observed pattern was consistent across the planned secondary measures. The registry also does not report a hierarchy among secondary endpoints or identify any confirmatory role for them.

Accordingly, secondary findings can add context but should not replace the primary comparison. The temperature result describes a difference in an intraoperative measure; it does not resolve whether the strategies differ in endoscopically detected injury. Without fuller outcome reporting and a stated multiplicity approach, secondary results are best regarded as supportive or exploratory rather than as independent confirmation of the primary question.

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

• Procedure Time
• Temperature
• Swallowing Impairment Score

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either had esophageal injury detected within the defined assessment window or did not. For a binary endpoint, one useful summary is the event risk in each group, and a direct contrast is the risk difference. The registry reports a risk difference of -0.018 for temperature monitoring relative to esophageal deviation. A negative value indicates that the observed event risk was lower in the group named in the comparison than in the reference group. The comparison is unadjusted, so it does not account for other variables.

What does a risk difference describe?

General: A risk difference is the event risk in one group minus the event risk in the other. It is expressed on an absolute scale, so it describes the separation between group risks rather than the proportional change relative to one group. A value of zero represents no difference on this scale. The registry’s confidence interval for the primary risk difference spans negative and positive values, so the data are compatible with different directions of association. The event counts and group sizes are small enough that the estimate should be read with its uncertainty, not in isolation.

How do relative measures differ?

General: A risk ratio compares the event risks by division, while an odds ratio compares the odds of the event. These are relative measures and do not describe the absolute number of events by themselves. The registry reports both for the primary contrast, with intervals that include values on either side of no relative difference. Because the event is uncommon in the posted groups, the numerical size of a relative measure can look different from the absolute risk difference. No single measure should be read without its interval and the underlying group counts.

What does the p-value mean?

General: A p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it is not a measure of clinical importance. For the primary comparison, the registry reports an unadjusted p-value of 0.828. This value does not provide strong evidence against a no-difference null under the stated comparison. It does not show that the groups are equivalent, and it does not measure the probability that the observed direction will recur.

The temperature comparison is a difference between group means. The registry reports means and standard deviations, along with a mean difference of 0.84 and an unadjusted p-value of <0.001. General: A standard deviation describes variation among individual observations around a group mean; it is not the same as the uncertainty in the mean. A confidence interval for a mean difference describes uncertainty in the estimated contrast under the analysis assumptions. It is distinct from a range containing most individual observations.

Why does over-dispersion matter?

General: Over-dispersion occurs when variation in the observed data exceeds what a statistical model assumes. In count outcomes, for example, a simple model may expect a particular relationship between the mean and variance; extra variability can make standard errors too small if it is ignored. This can make confidence intervals too narrow and p-values too optimistic. The primary endpoint is posted as a participant count with an event, rather than as a repeated event rate or a count process. The registry does not report an over-dispersion assessment or model for this endpoint, so no such adjustment can be inferred.

The primary comparison is reported as unadjusted. The registry record does not report covariate-adjusted models, subgroup analyses, interim analyses, or the prespecified statistical analysis plan. Without those details, the posted comparison should be interpreted as the analysis recorded in the results rather than assumed to represent a particular adjustment strategy. The registry also lists no reported secondary analyses.

The posted analysis population excludes 17 roll-in patients and two pre-procedure withdrawals. That is important because the randomized trial’s stated enrollment and the primary analysis groups describe different aspects of the record. Details of whether the analysis followed intention-to-treat principles, how missing outcomes were handled, or whether any participants were excluded for additional reasons are not reported in the registry record.

General: Randomization can support a causal comparison when assignment is implemented as planned and analysis preserves the assigned groups, but it does not remove uncertainty, missing-data concerns, or problems arising after randomization. The record identifies the trial as randomized, but does not supply enough analysis detail to establish exactly how those issues were addressed. Statistical interpretation should therefore stay close to the posted counts, contrasts, and intervals.

11. Confidence Intervals and Precision

Confidence intervals express uncertainty around an estimated contrast. General: A confidence interval is generated by a statistical procedure that, under its assumptions, would cover the target parameter at the stated rate over repeated studies. It is not a range that assigns a probability to the true value after the data have been observed. A narrower interval indicates greater precision; a wider interval indicates less precision.

For the primary risk difference, the registry’s interval includes negative and positive values. This means the estimate is compatible with a lower observed event risk in either group, and with no difference. The interval is broad relative to the point estimate, so the direction and size of any underlying difference are uncertain. The unadjusted p-value of 0.828 is consistent with that lack of a clear separation from no difference; it does not establish equivalence.

The counts underlying the primary contrast are 5.0 events among 36.0 participants in the deviation group and 4.0 among 33.0 in the monitoring group. With relatively few events in the posted results, each event contributes meaningful information to the comparison. Consequently, the primary estimate is not precise enough to support a narrow conclusion about the size or direction of a difference.

The temperature mean-difference interval, by contrast, lies entirely on one side of no difference, and the unadjusted p-value is <0.001. This indicates greater statistical separation for that secondary measure in the posted data. It does not change the uncertainty around the primary injury outcome, because the two outcomes measure different things.

Intervals depend on analysis assumptions, and the registry record does not report the complete statistical plan or additional sensitivity analyses. The posted intervals are therefore best understood as uncertainty under the reported comparisons, not as guarantees that capture all sources of uncertainty. Precision also should not be confused with importance: a precise estimate for a secondary measurement does not automatically answer the primary clinical question.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design justification. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The original trial’s sample-size assumptions are not reported in the registry record.

For the primary binary outcome, the planning figures are participants per arm. For example, planning for 100% of the observed effect gives 5,683 participants per arm for 80% power and 7,607 participants per arm for 90% power. Planning for 75% of the observed effect gives 10,249 participants per arm for 80% power and 13,720 participants per arm for 90% power. Planning for 50% of the observed effect gives 23,388 participants per arm for 80% power and 31,309 participants per arm for 90% power.

In plain terms, 80% power means that a study of the stated size would have an 80% chance of detecting the assumed effect at the stated significance level if that effect and the planning assumptions were true. The 90% column describes the corresponding planning target of a 90% chance. These are design targets, not guarantees for any particular trial. The figures are not observed power.

The pattern is that smaller effects require more participants to detect with the same power target. That is why the planning scenarios for smaller fractions of the observed effect call for larger groups. These figures should not be read as a recommendation or as a reconstruction of the original trial’s intended enrollment; they illustrate how sample-size requirements change under 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 = 0.139; treatment proportion p₁ = 0.121; average p̄ = 0.130.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4757 = 0.9323.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4755 = 0.4002.
4. n = (0.9323 + 0.4002)² / (-0.0177)² = 5,682.6, rounded up to 5,683 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 <- 0.138888888888889                          # control proportion
p1 <- 0.121212121212121                          # 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(1546168)
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 = 5,683 (80% power), 7,607 (90% power)
 75% of observed effect: n per arm = 10,249 (80% power), 13,720 (90% power)
 50% of observed effect: n per arm = 23,388 (80% power), 31,309 (90% power)
power.prop.test: 5682.6 
Simulated power at n = 5,683 per arm: 0.797 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the trial prespecified a multiplicity strategy. This matters because the record lists a primary endpoint and three secondary outcomes. When several outcomes are tested, the chance of at least one apparently notable result can increase if each is evaluated separately without adjustment. General: Multiplicity procedures can control that risk by adjusting significance thresholds or by specifying a hierarchy of tests. The appropriate approach depends on the study’s aims and analysis plan.

The temperature result is reported with an unadjusted p-value. No adjustment for multiple comparisons is reported in the registry record, and no outcome hierarchy is described. The result should therefore be interpreted as an unadjusted secondary finding, not as evidence that has been confirmed across a prespecified family of outcomes. Procedure time and swallowing impairment score are listed but their results are not reported in the registry record, further limiting a broad reading of the secondary outcomes.

Information about missing data is also limited. The primary outcome description states that 17 roll-in patients and two pre-procedure withdrawals were removed from the analysis. The registry does not give additional details about the number of missing endoscopy assessments, the reasons for any unavailable outcomes, or the methods used to handle missing data. It does not report sensitivity analyses that might show whether conclusions change under different assumptions about missing outcomes.

The record identifies a randomized design, but it does not state whether the primary analysis was intention-to-treat, per-protocol, or another analysis population. Nor does it report whether participants were analyzed according to randomized assignment. The stated exclusions are relevant to understanding the analyzed group, but they are not enough to determine the full analysis strategy.

Interim analyses, stopping rules, the original statistical analysis plan, and the sample-size justification are not reported in the registry record. The terminated status is recorded, but no reason for termination is reported. These omissions prevent a full assessment of whether the posted analyses match prespecified decisions or whether changes were made during the trial.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pericardial effusion (6.1%), asthma exacerbation (3.0%), pneumonia (2.8%).

The registry reports serious adverse events for 2 participants among 36 at risk in the esophageal-deviation group and 3 among 33 at risk in the temperature-monitoring group. Other adverse events are reported for 7 among 36 at risk in the deviation group and 4 among 33 at risk in the monitoring group. Deaths are recorded as 0 in both groups.

These figures describe the posted event counts and the corresponding numbers at risk. They do not by themselves establish whether a difference between groups is meaningful. Safety comparisons require attention to event definitions, follow-up duration, severity, and uncertainty. The registry record does not give enough detail in these summary figures to determine the clinical significance of individual events or to estimate a precise comparative safety effect.

The registry lists Pericardial Effusion at 6.1%, Asthma Exacerbation at 3.0%, and Pneumonia at 2.8% among the top serious adverse event terms. The record does not clarify the denominators or group allocation for these term-specific percentages, so they should not be assigned to a particular trial arm on the basis of the posted summary. Adverse-event counts are distinct from the primary endpoint, which is endoscopically assessed esophageal injury.

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

The primary results describe a randomized comparison of esophageal deviation with an IDE device against luminal temperature monitoring alone during AF ablation. Endoscopically detected injury within 1 week was recorded in 5.0 participants in the deviation group and 4.0 in the monitoring group. The estimated risk difference was -0.018, with an unadjusted p-value of 0.828. The interval around that estimate includes negative and positive values, leaving substantial uncertainty about the direction and size of any difference.

These data do not establish that the interventions produce the same injury risk. A non-significant result is not proof of equivalence or non-inferiority; those conclusions require an appropriate design, prespecified margins, and analyses. The registry record does not report an equivalence or non-inferiority framework. Nor does the comparison show that either approach is better, because the primary estimate is imprecise and does not clearly separate the groups.

The results also do not determine the overall safety of either approach. The adverse-event summaries give counts, but limited detail is reported about event timing, severity, or the comparative analysis. The listed deaths are 0 in both groups, but this does not resolve the interpretation of other adverse events or establish safety across broader populations and settings.

The temperature outcome is a secondary intraoperative measurement and has a more distinct unadjusted statistical contrast. It addresses a different question from whether injury was detected by endoscopy. The registry does not report results for procedure time or swallowing impairment score, so the posted results are not a complete account of the listed outcomes.

In general, a randomized trial can inform a causal comparison when its design and analysis are appropriately implemented. The registry record does not report enough detail about allocation methods, analysis populations, missing data, or the statistical plan to assess all those conditions. The findings therefore describe the posted results in the analyzed participants; they should not be extended beyond that evidence or interpreted as medical advice.

17. Why This Trial Matters Statistically

This trial illustrates a central issue in clinical biostatistics: the observed direction of an estimate and the strength of evidence about that estimate are not the same thing. The primary point estimate has a numerical direction, but its confidence interval crosses from negative to positive values and the unadjusted p-value is 0.828. Reading the count alone would miss the uncertainty; reading the p-value alone would miss both the estimated direction and the limited precision.

The endpoint is also a useful example of how a clinically direct outcome can still produce an inconclusive comparison. Endoscopic injury is the primary outcome named by the registry, and the stated assessment window is within 1 week. Yet the posted event counts are limited, so the estimate cannot sharply distinguish between potentially different effects. The design’s randomized label does not guarantee a precise result.

The contrast between the primary and secondary results reinforces the importance of outcome hierarchy. Temperature shows a more distinct statistical difference in the posted results, but it is not the primary injury endpoint. A statistically notable secondary result cannot answer a different primary question, particularly when other listed secondary results are not reported and multiplicity handling is not described.

The planning illustrations also show how assumed effect size changes the sample size needed for a chosen power target. They are based on the observed effect and explicit planning assumptions, and are not the original design justification. Keeping those planning calculations separate from what the trial actually observed helps prevent a common misreading: a trial’s results are not validated by retrospectively attaching an observed-power figure.

Finally, the record demonstrates the value of transparent reporting. Details about masking, analysis populations, missing outcomes, multiplicity, and the reason for termination are important to interpretation but are not reported. Statistical conclusions depend not only on numerical results, but also on knowing how outcomes and analyses were defined and handled.

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.

The primary comparison is based on 5.0 and 4.0 observed injury events in groups of 36.0 and 33.0 participants, respectively. The confidence interval spans both directions of effect, indicating limited precision. The registry status is terminated, but the reason for termination is not reported in the registry record. The listed enrollment is 88, while the primary analysis description specifies exclusions; further participant-flow detail is not reported.

The assessment window and method are specified, but the record does not report whether every participant received endoscopy or how missing assessments were handled. It also does not explain whether injury severity was recorded or whether events were independently adjudicated. These details would help assess endpoint ascertainment and the meaning of a binary presence-or-absence outcome.

Although the trial is described as double-blind, who was masked and how the masking worked are not reported in the registry record. Randomization methods and allocation concealment are also not described. The registry does not report whether the primary comparison followed randomized assignment or used a different analysis population. The statement about excluding roll-in patients and withdrawals does not resolve those questions.

The record lists procedure time and swallowing impairment score, but results for those outcomes are not reported. A multiplicity plan, interim analyses, the original sample-size justification, and a full statistical analysis plan are also not reported in the registry record. The secondary temperature result is unadjusted, so its interpretation should account for the possibility of multiple comparisons.

Finally, the registered study concerns the stated AF ablation setting and the participants included in its analysis. The posted information alone does not establish how results apply to other populations, procedures, or clinical settings. These limitations affect the strength and scope of statistical interpretation; they do not change the numerical results recorded for the analyzed groups.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Deviating the Esophagus in Atrial Fibrillation Ablation — NCT01546168.
• Registry record last updated 2018-01-23; status last verified 2018-01.
• Results first posted 2018-01-23.
• 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

NCT01546168 is a randomized, double-blind, parallel-group study of esophageal deviation versus luminal esophageal temperature monitoring during AF ablation. The registry lists enrollment of 88, a terminated status, study start in 2011-11, and primary completion in 2015-12.

The primary endpoint was the number of participants with esophageal injury on upper gastrointestinal endoscopy within 1 week. The posted counts were 5.0 among 36.0 participants with deviation and 4.0 among 33.0 with temperature monitoring. The registry reports a risk difference of -0.018 and an unadjusted p-value of 0.828; the interval includes values in both directions, so the primary comparison remains uncertain.

Temperature was the only secondary outcome with posted results. Procedure time and swallowing impairment score results, the reason for termination, and further details of the analysis plan and missing data are not reported in the registry record.