Esophageal Cooling for AF Ablation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Esophageal Cooling for AF Ablation (NCT03691571), a randomized na study. The primary outcome is Number and Percentage of Participants With Esophageal Thermal Injury.

2. Clinical Question

The registry describes a randomized comparison of device-based esophageal cooling with standard temperature monitoring. Its stated purpose was to determine whether cooling limits the number or seriousness of esophageal injuries during atrial fibrillation ablation. The posted primary outcome concerns whether an injury occurred, rather than a graded measure of injury seriousness: it is the count of participants with any injury measured by EGD.

The outcome figures record 8 participants with injury in the esophageal-cooling arm and 5 in the control arm, with 22 participants recorded in each arm for this outcome. The posted comparison therefore describes a higher observed event count in the cooling arm. The uncertainty around that contrast is important: the recalculated risk-difference interval includes values on either side of no difference, and the sponsor-reported test is p > .05. These data do not establish that cooling increased injury, nor do they establish that it reduced injury.

The registry lists an enrollment of 55, while the primary outcome figures are reported for 22 per arm and a total of 44. The registry record does not explain this difference or give the primary analysis population definition. The clinical question can therefore be stated clearly, while the relationship between enrollment and the posted outcome counts remains unreported.

3. Trial Design

NCT03691571, titled Esophageal Cooling for AF Ablation, is a completed randomized, single-masked, parallel-group study sponsored by the University of Pennsylvania. The official title is Utility of Esophageal Cooling Therapy for the Prevention of Thermal Injury During Atrial Fibrillation Ablation (eCoolAF). The registry lists the phase as NA and the condition as atrial fibrillation.

One arm received esophageal cooling with the EnsoETM device; the comparison arm received standard-of-care treatment described as standard temperature-probe monitoring. The registry describes the device intervention and comparator but does not identify who was masked. Further details of allocation concealment, the randomization procedure, procedural implementation, or masking maintenance are not reported in the registry record.

The registry lists enrollment as 55, a study start date of 2018-10-11, a primary completion date of 2020-03-25, and status as completed. The posted primary outcome data list 22 participants in each arm and a total of 44 for that outcome. The record does not explain the difference between the enrollment figure and these outcome counts, or report why outcome data are not listed for everyone included in the enrollment figure. The timing of the primary outcome is Day 1 to 2.

Five outcome measures and four analyses are recorded overall, while three secondary outcomes are posted. The available secondary outcomes include posterior-wall ablation temperature, another posterior-wall ablation parameter measured in ohms, and acute PV reconnection. No further detail on a formal analysis plan, sample-size justification, or the trial's original design assumptions is reported in the registry record. The sample-size illustrations associated with the observed results are separate planning calculations, not a record of how the trial was designed.

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 55 enrolled patients, 11 patients withdrew from the study prior to completing the post-procedure endocervical glandular dysplasia (EGD) due to delays obtaining the EGD prior to discharge.

Overall Study

Reasons for not completing this period:

5. Baseline Characteristics

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

Population: Fifty-five patients were enrolled in the study with 31 patients randomized to the device group and 24 patients randomized to the control group. Eleven patients withdrew from the study prior to completing the post-procedure EGD due to delays obtaining the EGD prior to discharge and 44 patients completed the study.

6. Primary Endpoint

The registry lists the primary outcome as Number and Percentage of Participants With Esophageal Thermal Injury, measured over Day 1 to 2.

The primary endpoint is the number of participants with any esophageal thermal injury, measured by EGD on Day 1 to 2. It is a binary outcome at the participant level: each participant is represented as having an injury or not having an injury for the purpose of the count. The registry labels the measure as a count of participants and describes it as an occurrence rate measured by EGD.

EGD is the stated assessment method for detecting injury. Counting participants with an event gives a direct summary of how often an injury was observed in each randomized arm during the stated assessment window. Comparing those counts, while accounting for the number assessed in each arm, provides an interpretable contrast between the cooling strategy and standard temperature-probe monitoring. A risk difference expresses that contrast as the difference in event proportions between arms; an interval around the estimate communicates how uncertain that comparison is.

The endpoint captures occurrence of any injury, not its severity or a detailed injury score. Although the study purpose refers to limiting the number or seriousness of injury, the posted primary endpoint does not separately quantify seriousness. The registry record does not report the EGD grading criteria, assessor blinding, or a more detailed definition of what qualified as injury. Those details would help readers understand how consistently the event was identified and whether different degrees of injury were combined.

The primary endpoint figures list 8 events among 22 participants in the cooling arm and 5 among 22 in control. The observed difference is not, by itself, proof of a true difference between the strategies. The accompanying uncertainty and the sponsor's reported test are relevant to interpreting the small set of observed events.

7. Results Posted in the Registry

• Esophageal Cooling: 36.4% (8/22) versus 22.7% (5/22) on control; risk difference 13.6 percentage points (95% CI -13.0 to 40.3), risk ratio 1.60 (0.62–4.13); unadjusted two-proportion z-test p = 0.322.

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.

Posterior Wall Ablation Parameters: 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:
  • Esophageal Cooling: mean 25.00 versus 25.70 on control; difference -0.70 (95% CI -1.59 to 0.19), standardized effect d = -0.47; z-test p = 0.122.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Esophageal Cooling and the control. The interval gives the range of effects that remain compatible with the data.

Posterior Wall Ablation Parameters

• 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:
  • Esophageal Cooling: mean 10.00 versus 10.00 on control; difference 0.00 (95% CI -1.18 to 1.18), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Esophageal Cooling and the control. The interval gives the range of effects that remain compatible with the data.

Occurrence of Acute PV Reconnection

• 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:
  • Esophageal Cooling: 27.3% (6/22) versus 4.5% (1/22) on control; risk difference 22.7 percentage points (95% CI 2.2 to 43.3), risk ratio 6.00 (0.79–45.81); unadjusted two-proportion z-test p = 0.039.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Esophageal Cooling than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Across the secondary outcomes, the results do not present one consistent pattern that independently settles the primary question. The measures cover procedural characteristics and an acute event, and their scales and analysis methods differ. The registry reports analyses for the continuous measures using Wilcoxon (Mann-Whitney) tests and for the binary event using Fisher Exact. The posted recalculations and sponsor-reported tests are not necessarily identical analyses, so they should be interpreted with their methods in view.

These outcomes can add context about what was measured during the procedure, but they do not directly replace the primary endpoint, which is esophageal thermal injury on Day 1 to 2. A secondary procedural measure may describe a different feature of the ablation, while an acute event is not itself a direct assessment of esophageal injury. The primary result therefore remains the central comparison for the stated question about thermal injury.

Multiplicity also matters. When several outcomes are examined, an isolated result may appear notable by chance, even when there is no underlying difference. The registry does not report a multiplicity adjustment or a hierarchical testing strategy. As a result, unadjusted secondary p-values carry less confirmatory weight than a clearly prespecified primary analysis with an explicitly reported testing plan. This does not make secondary outcomes useless; they can inform future questions and help describe the data, but they should be regarded as supportive or exploratory unless a stronger analysis plan is documented.

The total pattern should be read as a set of distinct observations with differing uncertainty, rather than as a vote in which the number of statistically notable results determines the conclusion. No secondary result resolves the imprecision of the primary comparison, and none establishes the presence or absence of a clinically important effect. The registry record does not report a broader prespecified interpretation framework for these outcomes.

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

• Posterior Wall Ablation Parameters: Temperature
• Posterior Wall Ablation Parameters
• Occurrence of Acute PV Reconnection

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference describe?

A risk difference compares the proportion of participants with an event in one arm with the proportion in the other arm. It is expressed on the same scale as the event proportions, so zero represents no difference in those observed proportions. A positive or negative estimate indicates the direction of the observed contrast according to the order used for the comparison. For the primary endpoint, the posted recalculation gives a risk difference of 0.136 for esophageal cooling relative to control. This is an unadjusted comparison based on the outcome counts recorded in the two arms.

A risk difference is a descriptive contrast, not a causal guarantee. Random assignment supports a comparison between allocated groups, but interpretation still depends on how outcomes were measured, which participants contributed data, and whether the analysis followed the planned approach. Those details are not all reported in the registry record.

What does a confidence interval communicate?

A confidence interval presents a range of estimates compatible with the data under the calculation's assumptions. It communicates precision as well as direction: a narrow interval indicates that the estimate is more tightly determined, while a wide interval leaves more uncertainty about the magnitude and potentially the direction of the difference. The primary risk-difference interval runs from -0.130 to 0.403. Because it includes zero, it does not rule out no difference under the interval calculation. Its span also includes both negative and positive values, so the data do not sharply distinguish the direction of the underlying contrast.

A confidence interval is not a list of outcomes that each have an equal probability of being true, and it does not establish clinical importance. The registry does not state the confidence level for the recalculated interval. It is therefore appropriate to describe the endpoints as the reported interval bounds without assigning a confidence level not documented in the record.

How should p-values be read?

A p-value measures how compatible the observed data are with a specified null model, assuming that model and the test's conditions. It does not give the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The primary outcome's recalculated unadjusted p-value is 0.322; the sponsor's reported Fisher Exact result is p > .05. Both are consistent with the sponsor's report not identifying a statistically significant primary comparison at the conventional .05 threshold, but the registry does not report a prespecified significance threshold for the trial's primary analysis.

The recalculated and sponsor-reported values come from different presentations of the analysis. The recalculation uses posted summary counts and an unadjusted method, while the registry identifies the sponsor's test as Fisher Exact. The methods and assumptions matter when comparing p-values; they should not be treated as interchangeable values from an identical calculation.

Why might a binary outcome use Fisher's exact test?

For a binary outcome, a test compares the distribution of event and non-event counts between groups. Fisher's exact test is one method for evaluating such a comparison and is commonly applicable to count data, including settings with relatively few events. It evaluates the observed arrangement of counts under its null model. The registry reports this method for the primary analysis. It does not report further details about the sponsor's analysis implementation or any adjustment variables.

Why does the mean difference matter for continuous measures?

For a continuous outcome, an arm mean summarizes the average observed value, and a mean difference compares the two arm means. The posted posterior-wall temperature means are 25.0 for cooling and 25.7 for control; the recalculated mean difference is -0.7, with an interval from -1.586 to 0.186. The other posterior-wall parameter has a mean of 10.0 in each arm, with a recalculated mean difference of 0.0 and an interval from -1.182 to 1.182.

The reported standard deviations describe spread among the observed measurements within each group. They are not confidence intervals for the group means. The registry lists the Wilcoxon (Mann-Whitney) test for each continuous comparison. This rank-based test compares the distributions of observations between groups; it is not exactly the same question as a test of the difference in means. The recalculated mean differences provide a simple summary from the posted means, while the sponsor's reported test is based on ranks. Accordingly, the p-values from the sponsor tests need not match those from a mean-based calculation.

What does over-dispersion mean in general?

In general, over-dispersion occurs when observed variation is greater than a statistical model assumes. If a model understates variability, standard errors can be too small and uncertainty can appear narrower than it should be. This concept is relevant to count models and some clustered or repeated-measure settings. The registry does not report an over-dispersion assessment or indicate that a count model was used for these endpoints. The primary outcome is posted as a count of participants with an event, and its reported sponsor analysis is Fisher Exact; there is no basis in the registry record to claim that over-dispersion was present or that it affected the primary result.

Why do analysis populations and multiplicity matter?

In general, an analysis population specifies which randomized participants contribute to an endpoint analysis, while multiplicity refers to the increased chance of false-positive findings when many outcomes or comparisons are tested. A prespecified approach can clarify which result is primary and how secondary analyses should be interpreted. The registry identifies the primary outcome and lists multiple secondary measures, but does not report the analysis population definition, missing-data method, or multiplicity adjustment. These omissions limit how fully the posted comparisons can be evaluated as a complete statistical plan.

11. Confidence Intervals and Precision

Precision concerns how tightly the data estimate the comparison, rather than whether the observed direction is favorable or unfavorable. The primary risk-difference estimate is 0.136, and its reported interval runs from -0.130 to 0.403. Because the interval includes zero and extends in both directions, the result is compatible with no difference as well as with differences in either direction under the calculation. The breadth of that interval indicates substantial uncertainty about the magnitude of the primary contrast.

The event counts are modest, and the intervals for the secondary binary comparison of acute PV reconnection are also broad: the reported risk-difference interval is 0.022 to 0.433. Its recalculated unadjusted p-value is 0.039, whereas the sponsor-reported Fisher Exact p-value is 0.10. The difference between these analyses is a reminder that inferential results can depend on the statistical method, particularly with limited event counts. The sponsor-reported analysis should be distinguished from the unadjusted recalculation rather than collapsed into a single conclusion.

For the continuous posterior-wall outcomes, the recalculated intervals likewise express uncertainty about the mean differences. The temperature interval ranges from -1.586 to 0.186, and the ohms interval ranges from -1.182 to 1.182. These bounds do not establish that the underlying values are identical; they show the range of contrasts supported by the posted summary data under the recalculations.

The registry does not state the confidence level for these recalculated intervals. They should therefore be read as the posted interval estimates, without assigning a confidence level not specified in the record. In all cases, intervals quantify statistical uncertainty under a method; they do not address whether a difference would be clinically important. The registry does not report a threshold for clinical importance.

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 a report of the trial's original design calculation. For the binary outcomes, the figures are participants per arm. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The target effect is a stated fraction of the observed effect. The registry record does not report the trial's own original sample-size assumptions or justification.

The column for 80% power gives the planned number of participants per arm for a future study to have an 80% chance of detecting the assumed effect under the listed assumptions, if that effect and those assumptions are appropriate. The 90% power column gives the corresponding planning figure for a 90% chance. Higher target power generally requires more participants for the same assumed effect.

Rows that plan for 75% or 50% of the observed effect assume a smaller effect than the row based on 100% of the observed effect. Smaller effects are harder to distinguish from chance variation, so the illustrations call for more participants per arm as the assumed effect becomes smaller. These numbers are planning illustrations, not observed power for this completed trial.

The calculations are sensitive to the observed effect, which can be unstable when based on a modest dataset. The figures should not be interpreted as evidence that a future study will have exactly the listed performance: actual precision and power depend on the true effect, event frequency, missing data, and analysis choices. The assumptions also use a normal approximation, while the registry reports Fisher Exact analyses for the binary outcomes. The illustrations are therefore best understood as a simplified planning aid, not as a substitute for a trial-specific design calculation.

For the continuous outcomes, the same stated planning conventions apply, with participant counts per arm. The registry's note reserves total-event reporting for time-to-event tables; the posted outcomes are not identified as time-to-event measures. The sample-size illustrations should be read alongside the uncertainty intervals and the limited outcome counts, not as a verdict on the adequacy of the completed trial.

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 = 0.227; treatment proportion p₁ = 0.364; average p̄ = 0.295.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6452 = 1.2646.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6380 = 0.5369.
4. n = (1.2646 + 0.5369)² / (0.1364)² = 174.5, rounded up to 175 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 <- 0.227272727272727                          # control proportion
p1 <- 0.363636363636364                          # 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(3691571)
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 = 175 (80% power), 234 (90% power)
 75% of observed effect: n per arm = 301 (80% power), 402 (90% power)
 50% of observed effect: n per arm = 651 (80% power), 871 (90% power)
power.prop.test: 174.5 
Simulated power at n = 175 per arm: 0.805 (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

For the primary outcome, the registry reports the sponsor's analysis as Fisher Exact with p > .05. A separate unadjusted recalculation from the posted event counts gives p = 0.322 and a risk-difference estimate of 0.136, with an interval from -0.130 to 0.403. The sponsor's result and the recalculation are not identical statistical summaries: the sponsor's method is explicitly reported as Fisher Exact, while the recalculated contrast is an unadjusted summary based on the posted counts.

The sponsor result does not report an effect estimate or interval, so it cannot replace the estimate-and-interval description of the size and precision of the observed contrast. Conversely, the recalculation does not replace the sponsor's own inferential analysis. The registry record does not describe additional details of the sponsor's test, adjustments, or analysis population. In reading the results, it is useful to keep the reported analysis and the recalculation distinct and to note that neither establishes a statistically significant primary difference.

The discrepancy flag is false. The record does not identify a conflict between the posted primary figures and the sponsor analysis. The sponsor's p-value is reported only as greater than .05, rather than as an exact p-value. The recalculated p-value offers a more specific unadjusted summary, but should not be mistaken for the sponsor's reported result.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and records multiple secondary outcome measures. It does not report whether statistical testing across those outcomes was adjusted for multiplicity, whether a hierarchy of hypotheses was prespecified, or whether secondary outcomes were intended to be confirmatory or exploratory. Without this information, individual unadjusted secondary p-values should be interpreted cautiously. Testing several outcomes can increase the chance that at least one result appears notable through random variation, even when no true difference exists.

The analysis population for the primary and secondary outcomes is not reported in detail. The primary figures list 22 participants in each arm and a total of 44, whereas the registry lists enrollment as 55. The registry record does not explain the relationship between these figures or identify the reasons for participants not appearing in the posted primary outcome counts. It also does not report whether the analysis followed intention-to-treat, per-protocol, or another population definition. No assumption should be made about which participants were excluded or why.

Missing-data handling is not reported in the registry record. The record does not describe the extent, timing, or reasons for missing endpoint assessments, nor whether any imputation or sensitivity analysis was used. This matters because an outcome count can be difficult to interpret if the participants assessed differ systematically from those without an observed assessment. The EGD assessment window is reported as Day 1 to 2, but the registry does not provide a participant-flow account or further detail on assessment completion.

Interim analyses and stopping rules are not reported. The registry also does not report the trial's original sample-size assumptions or a detailed statistical analysis plan. These omissions do not demonstrate that such procedures were absent; they mean that their use cannot be established from the registry record. The posted primary and secondary results are therefore best read with attention to what is documented and with appropriate restraint about unreported analysis decisions.

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 posted serious adverse event figures list zero serious adverse events among 22 participants at risk in the esophageal-cooling arm and zero among 22 at risk in control. The registry also records zero deaths in each arm. These are the serious-event counts listed for the posted safety data.

Zero reported serious events in these groups does not establish that serious harms cannot occur, nor does it rule out differences in uncommon harms. A trial with limited safety counts may be unable to characterize rare events precisely. The registry does not provide a list of serious adverse event terms, and the top serious terms field is empty. It also does not provide a detailed account of safety ascertainment or the relationship, if any, of other events to the device or procedure.

The record lists other adverse events in 10 participants at risk in the cooling arm and 9 at risk in control. These are distinct from the serious adverse event figures and should not be conflated with them. The registry record does not report further detail in this safety summary that would establish the type or clinical significance of those other events. The figures describe what is posted; they do not, by themselves, establish comparative safety.

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

The primary result describes the observed frequency of esophageal thermal injury assessed by EGD on Day 1 to 2. More events were recorded in the cooling arm than in control, but the uncertainty interval for the recalculated risk difference includes no difference and extends in both directions. The sponsor-reported Fisher Exact analysis is p > .05. The data therefore do not establish a statistically significant difference in the primary endpoint, and the uncertainty leaves the size and direction of any underlying difference unresolved.

This is not evidence that the two approaches are equivalent. A nonsignificant test does not prove that effects are identical or that any difference is too small to matter. Establishing equivalence or noninferiority generally requires prespecified margins and an analysis designed for that question; such margins and a noninferiority or equivalence framework are not reported in the registry record.

The results also do not establish that esophageal cooling increases injury. The observed direction is not enough to support that conclusion, particularly with a broad interval that includes negative values. Nor do these results establish that cooling prevents injury. The endpoint records whether any injury occurred and does not separately quantify injury seriousness. The stated study purpose included seriousness, but the posted primary measure is a participant count for any injury.

Secondary outcomes provide additional procedural and event measurements, but they have different meanings and methods and are not a substitute for the primary comparison. Because a multiplicity plan is not reported, isolated unadjusted secondary results should be treated cautiously. The posted data are most useful as a description of this trial's observed outcomes and their uncertainty, not as a definitive estimate of what would occur in other settings or populations.

Finally, the registry does not report the analysis population definition, detailed missing-data handling, outcome grading criteria, or the reasons for the difference between the enrollment figure and primary outcome counts. Those gaps limit assessment of how broadly the estimates represent enrolled participants. The results should be understood as uncertain evidence from the posted outcome data rather than a final determination about the comparative effects of the strategies.

18. Why This Trial Matters Statistically

This trial illustrates why an observed difference and a reliable conclusion are not the same thing. The primary endpoint has a directly interpretable form: the number of participants with any EGD-detected injury in each group. But the uncertainty interval around the risk difference is broad and includes no difference. A point estimate alone could invite an overly confident reading; the interval and the sponsor's reported analysis show why precision and inferential method need to be considered together.

It also illustrates the value of keeping reported analyses separate from simple recalculations. The registry reports Fisher Exact for the primary comparison, while the posted recalculation supplies a risk difference and an unadjusted p-value based on the summary counts. These summaries answer related but not identical statistical questions. Reporting both can help readers understand effect size and uncertainty without treating a recalculation as a substitute for the sponsor's analysis.

The study's secondary outcomes show another general statistical issue: a set of outcomes can be informative without each being equally confirmatory. Differences in outcome type bring different analysis methods, and multiple unadjusted tests raise the possibility of chance findings. A clear account of multiplicity, populations, and missing data would help readers judge the strength of evidence across endpoints; those details are not reported in the registry record.

Finally, the contrast between the registry enrollment figure and the primary outcome counts highlights the importance of participant flow. Readers need to know which participants contributed data and why other enrolled participants may not appear in an outcome analysis. The posted record allows the primary outcome to be described, but leaves that context unresolved. These are important considerations for interpreting any small clinical trial, especially when event counts and intervals convey substantial uncertainty.

19. Limitations

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

Several limitations specific to this record constrain interpretation. The registry lists enrollment as 55, while the primary outcome is reported for 22 participants per arm and a total of 44. The record does not explain the difference, describe participant flow, or state why the outcome counts do not cover the enrollment figure. The analysis population and missing-data methods are not reported, so the effect of unobserved outcomes cannot be assessed.

The primary endpoint is described as any injury measured by EGD on Day 1 to 2, but the registry does not report diagnostic or grading criteria, assessor masking, or how seriousness was defined. As a result, the posted primary measure does not tell readers how injury severity was classified, despite the study purpose referring to both number and seriousness of injury.

The primary event counts are limited, and the risk-difference interval is broad. The estimate is therefore imprecise and does not establish the direction of a true difference. The sponsor-reported primary analysis gives p > .05 but does not provide an effect estimate or interval, while the recalculation is unadjusted. The registry record does not report details that would fully reconcile the analytic approaches or establish a prespecified analysis plan.

There are multiple secondary outcomes, but multiplicity handling, interim analyses, original sample-size assumptions, and the trial's statistical analysis plan are not reported. The registry also does not report who was masked, allocation-concealment procedures, or further implementation details. These are gaps in the available record, not evidence that particular methods were or were not used. Together they warrant a cautious reading of both the primary comparison and secondary findings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Esophageal Cooling for AF Ablation — NCT03691571.
• Registry record last updated 2022-10-05; status last verified 2022-09.
• Results first posted 2021-12-21.
• 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

NCT03691571 is a completed randomized, single-masked, parallel-group trial sponsored by the University of Pennsylvania. It compared esophageal cooling with the EnsoETM device against standard temperature-probe monitoring during atrial fibrillation ablation. The registry lists enrollment of 55, a start date of 2018-10-11, and a primary completion date of 2020-03-25.

The primary outcome was any EGD-measured esophageal thermal injury on Day 1 to 2. The posted figures record 8 events among 22 participants in the cooling arm and 5 among 22 in control. The recalculated risk difference is 0.136, with an interval from -0.130 to 0.403; the sponsor reports Fisher Exact p > .05. The record does not explain the relationship between enrollment and the primary outcome counts.

Three secondary outcomes and safety figures are posted. Multiplicity handling, missing-data methods, the analysis population, and the original sample-size assumptions are not reported in the registry record. Overall, the primary comparison is imprecise and does not establish a difference between the study arms.