Prevention of Atrial Fibrillation Following Esophagectomy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Prevention of Atrial Fibrillation Following Esophagectomy (NCT00420017), a randomized phase 4 study. The primary outcome is Incidence of Atrial Fibrillation.

2. Clinical Question

The question is about a postoperative event recorded as a participant count, rather than a measure of how long each person remained in atrial fibrillation. The registry describes the primary analysis as per protocol, so the result pertains to that analysis population. It does not, on its own, describe every aspect of the treatment experience, such as timing or duration of events.

3. Trial Design

The registry describes a randomized, parallel-group, open-label Phase 4 trial sponsored by Indiana University. The study was marked completed. Its recorded start was 2005-09, and its primary completion was 2008-11. Enrollment was 80. The two listed arms were amiodarone and control, with 40 participants recorded in each arm.

The amiodarone arm received intravenous amiodarone. The control arm is described only as control; the specific control care is not reported in the registry record. Random allocation means that assignment was intended to use a chance-based process. A parallel design means participants were assigned to one group rather than crossing between the interventions. The masking field is none, so the record does not describe a masked trial.

The registry identifies the primary outcome as the incidence of atrial fibrillation, measured as the number of participants with the event during 7 days. Its population is designated per protocol. The listed secondary outcomes are length of post-surgical hospital stay, length of post-surgical intensive care unit stay, and the number of participants with adverse effects. The record lists four outcome measures and four analyses, but further detail about the additional measure or the analysis procedures is not reported in the registry record.

Although the record gives enrollment and group sizes, it does not report the trial’s own original sample-size assumptions or justification. Detailed eligibility criteria, allocation procedures, treatment schedule, and follow-up procedures are also not reported in the registry record. These gaps limit how fully the design and the relationship between planned and analyzed participants can be assessed from the registry entry alone.

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: 133 patients were screened for eligibility. 39 were excluded prior to consent d/t presence of exclusion criteria or declined participation. 94 were consented. 14 did not participate: 3 had pre-op exclusion criteria; 4 were withdrawn because the study protocol was delayed; 7 were excluded because they developed intra-operative atrial fibrillation

Overall Study

Analysis population for the primary outcome, as defined in the registry: Analysis was per protocol

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 Incidence of Atrial Fibrillation, measured over 7 days.

The primary endpoint is the number of participants who experienced atrial fibrillation following esophagectomy during 7 days. It is a binary outcome at the participant level: each participant either had the event during the stated timeframe or did not. The reported group counts are 6 in the amiodarone arm and 16 in the control arm. The registry states that the primary outcome analysis was per protocol.

This endpoint addresses the investigators’ central question about postoperative atrial fibrillation. Counting participants with an event offers a direct way to compare how often the event was observed in each group during the defined period. It does not describe the number of episodes per participant, the timing of an episode within that period, or its duration; those details are not reported in the registry record.

In general, a clearly defined timeframe helps specify which events contribute to an endpoint and makes the comparison interpretable. A binary endpoint also requires attention to the population analyzed and the completeness of event ascertainment. Further information about how atrial fibrillation was identified, how missing outcome data were handled, and whether any participants were excluded from the per-protocol analysis is not reported in the registry record. The endpoint therefore gives a focused measure of event occurrence, while leaving important measurement and analysis details unspecified.

7. Results Posted in the Registry

• Amiodarone: 15.0% (6/40) versus 40.0% (16/40) on control; risk difference -25.0 percentage points (95% CI -43.8 to -6.2), risk ratio 0.37 (0.16–0.86); unadjusted two-proportion z-test p = 0.012.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: the registry counts participants with atrial fibrillation during 7 days. For a binary outcome, the basic comparison can be expressed as a risk difference or a risk ratio. The risk difference subtracts the event proportion in one group from that in the other; the risk ratio divides one group’s event proportion by the other’s. These summaries answer related but distinct questions and use different scales. The posted results include a sponsor-reported risk ratio and an unadjusted recalculation expressed as a risk difference.

What does randomization contribute?

In general, randomization assigns participants to study groups by chance. Its purpose is to reduce systematic differences between groups at the start of a study, including differences that may not be measured. It does not guarantee that every potential confounder is balanced, especially in a study of limited size, and it cannot prevent bias arising after assignment. The registry identifies this trial as randomized but does not report the sequence-generation or allocation-concealment procedures. It is therefore possible to describe the design as randomized without making claims about how well assignment was protected from prediction or influence.

What does an open-label design mean?

The masking field is none. In general, an open-label design means treatment assignment is not masked from participants or study personnel. This can matter if awareness of assignment affects care, reporting, or the assessment of an outcome. The registry does not provide details about who assessed atrial fibrillation or whether outcome assessment followed a standardized procedure. The direction or size of any effect of open-label conduct cannot be inferred from the record.

How should the reported test and effect estimate be read?

The registry reports a chi-squared analysis for the risk ratio, with the estimate and confidence interval rounded in the record. A chi-squared test compares observed categorical counts with counts expected under a specified null hypothesis. The reported p-value summarizes the compatibility of the observed data with that null model, under the test assumptions. It is not a measure of effect size and does not indicate the probability that the null hypothesis is true. The unadjusted recalculation uses the posted summary counts to express the contrast as a risk difference. Because this is an unadjusted calculation, it should not be mistaken for a more detailed model-based analysis.

In general, binary-outcome methods rely on the recorded classifications and the analyzed population. A per-protocol analysis generally focuses on participants considered to have followed the assigned protocol, but the operational definition and exclusions used in this trial are not reported in the registry record. The record does not report an intention-to-treat analysis or explain how deviations from assigned treatment were handled. The listed group sizes and outcome counts do not by themselves reveal whether any participants were excluded from the per-protocol analysis.

Why do analysis choices matter?

Different effect measures can make a result easier to interpret for different questions. A risk difference describes the absolute separation between group event proportions, while a risk ratio describes their relative scale. Neither measure alone communicates all relevant context. Confidence intervals show a range of values compatible with the data and the method’s assumptions; they help assess precision, but do not account for biases that the design or analysis may introduce. A small p-value does not remove uncertainty about measurement, population selection, or generalizability.

Over-dispersion is a general concern for some count outcomes: observed variation can exceed what a simple model assumes, making standard errors too small if that extra variation is ignored. It is not an indicated issue for this primary endpoint as recorded, because the endpoint is a binary participant count, not a repeated count of episodes. The registry does not report a more elaborate model for the primary outcome, so no claim about such a model is warranted.

What is not described?

The registry lists four outcome measures and four analyses, but detailed methods for all outcomes, adjustment for multiple comparisons, missing-data procedures, and sensitivity analyses are not reported in the registry record. The original trial sample-size calculation, any interim analyses, and a full statistical analysis plan are also not reported in the registry record. Such details would help clarify which analyses were prespecified and how uncertainty was handled. Their absence from the record means that those features cannot be evaluated from the posted information.

10. Confidence Intervals and Precision

The registry’s reported risk ratio is 0.38, with a 95% confidence interval from 0.16 to 0.86. The interval gives a range of effect estimates compatible with the observed data under the analysis method and its assumptions. It is not a range containing a fixed percentage of individual outcomes, and it is not a statement that the true effect has a specified probability of falling within the interval.

For a risk ratio, 1 represents equal event proportions in the two groups. The reported interval lies below 1, so its range excludes that no-difference value. The interval nevertheless spans a range of possible relative effects; the point estimate alone would understate that uncertainty. The recalculated risk-difference interval also excludes zero, its no-difference value, though its endpoints are not repeated.

In general, confidence-interval width reflects both the amount of information in the data and the variability assumed by the method. A wider interval indicates less precision than a narrower interval on the same scale. Precision is not the same as validity: an interval can be narrow while systematic bias remains, and a confidence interval does not address limitations such as unclear outcome ascertainment, unreported exclusions, or incomplete follow-up.

The primary comparison is based on the registry’s per-protocol population description. Without details about missing observations or the exact analysis population, the interval’s practical scope is difficult to assess beyond that designation. It should be read as uncertainty around the reported group comparison, not as a guarantee that the same estimate would apply in other settings or populations.

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 figures are planning illustrations based on fractions of the observed effect, not the trial’s original design calculation. The original design assumptions are not reported in the registry record. For this binary endpoint, the listed figures are participants per arm, rather than total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect.

For planning at 100% of the observed effect, the illustration lists 49 participants per arm for 80% power and 65 participants per arm for 90% power. At 75% of the observed effect, it lists 94 participants per arm for 80% power and 125 participants per arm for 90% power. At 50% of the observed effect, it lists 224 participants per arm for 80% power and 299 participants per arm for 90% power.

In plain language, the 80% power column describes the planned group size associated with an 80% chance of detecting the specified effect under the stated assumptions, if that effect and the assumptions hold. The 90% column describes the corresponding planning target for a 90% chance. A smaller effect is harder to distinguish from random variation, so the illustration requires more participants per arm for smaller effects. These figures are not observed power and do not describe what the completed trial was designed to achieve.

The curve should be read as a visual representation of the same planning relationship, not as evidence that a particular effect will occur. Planning results depend on the assumptions and are not a substitute for the observed estimates and their confidence intervals.

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 = 0.400; treatment proportion p₁ = 0.150; average p̄ = 0.275.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6315 = 1.2377.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6062 = 0.5102.
4. n = (1.2377 + 0.5102)² / (-0.2500)² = 48.9, rounded up to 49 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 <- 0.4                          # control proportion
p1 <- 0.15                          # 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(420017)
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 = 49 (80% power), 65 (90% power)
 75% of observed effect: n per arm = 94 (80% power), 125 (90% power)
 50% of observed effect: n per arm = 224 (80% power), 299 (90% power)
power.prop.test: 48.9 
Simulated power at n = 49 per arm: 0.810 (20000 replicates)

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

13. Analyses Reported by the Sponsor

The registry’s own analysis reports a chi-squared risk ratio of 0.38, with a 95% confidence interval from 0.16 to 0.86 and p = 0.02. The unadjusted recalculation from the posted counts expresses the comparison as a risk difference of -0.25 and gives p = 0.012. These are not identical summaries: they use different effect measures, and the p-values are associated with their respective analyses.

The direction is consistent across the posted group counts, the sponsor-reported risk ratio, and the unadjusted risk-difference recalculation: the observed event count was lower in the amiodarone arm. The recalculation is useful as a transparent check based on the summary counts, but it does not replace the registry’s reported analysis. The registry does not provide enough detail to determine whether the sponsor’s procedure included adjustments beyond the stated chi-squared method.

The record does not mark a discrepancy between the sponsor analysis and recalculation. The sponsor result should therefore be understood as the reported trial analysis, while the recalculation is a separate unadjusted expression of the posted counts. Neither p-value should be treated as a measure of clinical importance or as a probability that the result is true.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists the primary outcome of atrial fibrillation and three secondary outcomes: hospital stay, intensive care unit stay, and adverse effects. It also lists four outcome measures and four analyses. The record does not explain how the four analyses correspond to the measures, whether all were prespecified, or whether any additional outcomes were assessed.

When several outcomes or comparisons are tested, the chance of obtaining at least one statistically notable result can increase. In general, multiplicity procedures may adjust the testing threshold or otherwise account for the number and structure of comparisons. No multiplicity adjustment or strategy for prioritizing outcomes is reported in the registry record. The reported primary-outcome p-value should therefore be read as the result of its stated analysis, without assuming that it accounts for testing across other outcomes.

Information about missing outcome data and participant flow through the analysis is also not reported in the registry record. The primary population is described as per protocol, but the criteria for that population and any exclusions are not specified. The posted arm sizes and event counts do not establish whether every randomized participant contributed to the analysis. No imputation method, missing-data sensitivity analysis, or intention-to-treat result is reported.

The record also does not report interim analyses, stopping rules, or a full statistical analysis plan. These details could clarify how decisions were made, which analysis was intended as primary, and how missing information and multiple outcomes were handled. Without them, it is not possible to evaluate those aspects of the trial from the registry record. This uncertainty does not change the arithmetic of the posted counts, but it limits assessment of the broader analysis process.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: death (5.0%).

The adverse-event entry reports serious adverse effects for 0 participants in the amiodarone arm and 2 participants in the control arm, with 40 participants at risk listed in each group. The entry also reports other adverse effects for 3 participants in the amiodarone arm and 1 participant in the control arm. These are counts in the registry record and should be read separately from the primary atrial fibrillation outcome.

The registry’s top serious-term listing includes “death” at 5.0%. Arm-specific death counts are not reported in the registry record. The listed term and percentage do not establish how deaths were distributed between groups, and should not be interpreted as an arm-specific death rate.

In general, adverse-event counts depend on how events were defined, collected, and classified, and a small number of reported events can leave substantial uncertainty about comparative safety. Definitions, severity criteria, timing, and the method used to attribute events are not reported in the registry record. The safety figures therefore describe the registry’s recorded counts, not a complete characterization of risk or a basis for medical advice.

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

The posted primary data show that fewer participants in the amiodarone arm were recorded with atrial fibrillation during 7 days than in the control arm: 6 of 40 compared with 16 of 40. The registry’s own analysis reports a risk ratio of 0.38, with a 95% confidence interval from 0.16 to 0.86 and p = 0.02. The unadjusted recalculation gives a risk difference of -0.25 and p = 0.012. These statistics describe the observed comparison using different measures.

The result does not, by itself, establish that the treatment works or does not work. Statistical evidence is not the same as certainty, and the confidence interval reflects uncertainty under the specified method rather than all possible sources of error. The trial was open-label, and key details about allocation, outcome assessment, adherence, missing data, and analysis population are not reported in the registry record. Those limitations matter when considering how much causal interpretation the comparison supports.

The primary endpoint addresses whether participants experienced atrial fibrillation within the recorded timeframe. It does not describe the number or duration of episodes, the timing of onset, or the full course of postoperative recovery. The registry lists hospital stay, intensive care unit stay, and adverse effects as secondary outcomes, but the information available does not provide detailed results for the length-of-stay outcomes. The safety counts are limited and lack detail about event definitions and ascertainment.

The findings also cannot be assumed to apply to other operations, patient groups, or care settings. The registry record describes a specific surgical context and does not provide enough detail to judge broader applicability. Readers should distinguish the observed group comparison from conclusions about clinical importance, long-term outcomes, or use in an individual patient. The statistics characterize this trial’s posted results; they are not medical advice.

17. Why This Trial Matters Statistically

This trial offers a clear example of why an outcome’s definition and analysis population matter. The primary endpoint is a participant count for atrial fibrillation during 7 days, and the record labels the analysis per protocol. The distinction between counting people with an event and counting repeated episodes is important: the posted result answers the former question, not the latter.

It also illustrates how one comparison can be expressed on different scales. The registry reports a risk ratio, while the unadjusted recalculation presents a risk difference. In general, relative and absolute measures can tell complementary stories, and both need to be read alongside uncertainty estimates. The presence of a p-value alone does not convey the size or precision of an effect, nor does it address the quality of outcome measurement.

The record also shows the limits of interpreting registry results when essential design and analysis details are absent. The trial is identified as randomized and open-label, but procedures for allocation, the per-protocol definition, handling of missing data, and multiplicity are not reported. That information is central to evaluating how faithfully the posted result represents the intended comparison.

Finally, sample-size planning is distinct from observed results. Illustrations based on fractions of the observed effect help show why smaller effects require larger planned groups under stated assumptions, but they do not reveal the trial’s original design rationale or its observed power. Keeping those ideas separate helps prevent over-reading a single completed trial’s statistics.

18. Limitations

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

Several trial-specific limitations follow from the limited registry detail. The study is described as randomized, but the method of sequence generation and allocation concealment is not reported in the registry record. Without those details, the protections against predictable or influenced assignment cannot be assessed. The masking field is none, so participants and study personnel were not masked according to the record. The record does not explain who assessed atrial fibrillation or what procedures were used to identify it.

The primary endpoint is described as per protocol, but the criteria for inclusion in that analysis and the handling of participants who did not follow the assigned intervention are not reported. Missing-data methods, participant flow, and a result based on all randomized participants are not reported in the registry record. This makes it difficult to judge whether the posted group sizes correspond to all randomized participants or only those included in the primary analysis.

The control intervention is described only as control, and details of the amiodarone regimen are not reported. The registry does not provide the original sample-size justification, interim analysis procedures, or full statistical analysis plan. It also does not report a multiplicity strategy for the primary and secondary outcomes. These omissions constrain assessment of prespecification and analysis choices.

Finally, the record provides limited information about adverse-event definitions, collection, and attribution, while arm-specific death counts are not reported. Detailed results for length of hospital and intensive care unit stay are not included in the posted outcome information. These limitations leave important questions about measurement, safety characterization, and the scope of inference unresolved.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Prevention of Atrial Fibrillation Following Esophagectomy — NCT00420017.
• Registry record last updated 2013-09-18; status last verified 2013-09.
• Results first posted 2013-02-06.
• 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

The registry record describes a completed, randomized, open-label, parallel-group Phase 4 trial sponsored by Indiana University. Enrollment was 80, with 40 participants listed in each arm. The intervention was intravenous amiodarone, compared with a control group.

The primary outcome was the number of participants with atrial fibrillation during 7 days, analyzed per protocol. The posted counts were 6 in the amiodarone arm and 16 in the control arm. The sponsor-reported analysis gives a risk ratio of 0.38, a 95% confidence interval from 0.16 to 0.86, and p = 0.02. The unadjusted recalculation expresses the contrast as a risk difference of -0.25 and gives p = 0.012.

Secondary outcomes include hospital stay, intensive care unit stay, and adverse effects. Further design, analysis, missing-data, multiplicity, and safety-reporting details are not reported in the registry record.