Curing Atrial Fibrillation in Heart Failure: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Curing Atrial Fibrillation in Heart Failure (NCT00292162), a randomized na study. The primary outcome is Change in Left Ventricular Ejection Fraction by Magnetic Resonance Imaging (MRI)%.

2. Clinical Question

The registry describes the study aim as establishing whether ablation in people with advanced heart failure and atrial fibrillation could result in marked improvement in heart function. The posted primary comparison is a difference in mean change between the randomized groups. It therefore addresses the relative change in this measured outcome, rather than every possible effect of treatment or every aspect of health. The registry lists secondary measurements of plasma B-type natriuretic peptide (BNP), including baseline and 6-month measurements. Those measures provide additional information, but they do not replace the primary question about MRI-based ejection fraction.

3. Trial Design

The registry record identifies this as a randomized, parallel-group study with no masking. It lists an enrollment of 41 and a completed status. The sponsor is NHS Greater Glasgow and Clyde. The study compared radiofrequency ablation with medical therapy in people with chronic heart failure and atrial fibrillation. The record describes ablation as pulmonary-vein isolation and the comparator as standard heart-failure therapy, with the listed medicines and possible additional diuretics or digoxin.

The primary outcome was change in MRI-measured left ventricular ejection fraction between baseline and 6 months. The registry reports 19 participants analyzed in each group for this outcome. It also notes that the number analyzed can differ from the number enrolled because some outcomes could not be measured, including when a participant did not tolerate MRI or dropped out. The reasons for missing primary measurements for particular participants are not reported in the registry record.

The posted results do not include a description of how the random sequence was generated, how treatment assignment was concealed, or how the study was organized across sites. Those design details are not reported in the registry record. The protocol’s original sample-size rationale and statistical analysis plan are also not reported in the registry record. Although the study is marked completed, the registry does not provide a reported analysis for the outcome comparisons. The comparison estimates discussed with the results are unadjusted recalculations from the posted group summary statistics, not a substitute for a sponsor-reported analysis.

The registry lists 41 participants enrolled, while analysis counts vary across outcomes. That distinction matters: enrollment describes the study population entered into the trial, whereas each outcome’s analysis count reflects the observations available for that particular measure. The primary endpoint counts are not identical to enrollment, and the BNP change analysis has its own counts. These differences mean that each estimate should be read alongside its outcome-specific analysis population rather than treated as though every enrolled participant contributed to every result.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Number of patients analyzed is different from number of patients enrolled because some of the outcomes could not be measured in some patients ie the patient did not tolerate an mri or dropped out of the study

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change in Left Ventricular Ejection Fraction by Magnetic Resonance Imaging (MRI)%, measured over baseline and 6 months.

The primary endpoint is change in left ventricular ejection fraction measured by magnetic resonance imaging from baseline to 6 months. Ejection fraction describes the proportion of blood ejected from the left ventricle in one heartbeat. The registry describes it as a measure of cardiac function. Measuring change allows the comparison to focus on how the outcome shifted over the stated follow-up interval, rather than comparing only the values at one time point.

MRI is the stated measurement method for this endpoint. The trial reports the mean change for each treatment group and the standard deviation, which describes variation in individual changes around each group mean. The medical-therapy group had a mean change of 2.8, with a standard deviation of 6.8, among 19 analyzed participants. The radiofrequency-ablation group had a mean change of 4.5, with a standard deviation of 11.1, among 19 analyzed participants. The unadjusted mean difference, comparing ablation with medical therapy, was 1.7.

This endpoint gives a focused measure of cardiac function, but it captures only one aspect of a complex clinical condition. It does not by itself describe symptoms, hospital use, survival, or all possible harms. The registry’s rationale identifies improvement in heart function as the study aim; the posted endpoint is the measured change in ejection fraction, not a broad assessment of every possible patient outcome.

7. Results Posted in the Registry

• Radiofrequency Ablation: mean 4.50 versus 2.80 on control; difference 1.70 (95% CI -4.15 to 7.55), standardized effect d = 0.18; z-test p = 0.569.

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.

Plasma B-type Natriuretic Peptide (BNP)

• 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:
  • Radiofrequency Ablation: mean -196.00 versus 85.00 on control; difference -281.00 (95% CI -991.00 to 429.00), standardized effect d = -0.24; z-test p = 0.438.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Radiofrequency Ablation and the control. The interval gives the range of effects that remain compatible with the data.

Plasma B-type Natriuretic Peptide (BNP) at Baseline

• 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:
  • Radiofrequency Ablation: mean 2,550 versus 1,846 on control; difference 704.00 (95% CI -524.82 to 1,933), standardized effect d = 0.36; z-test p = 0.261.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Radiofrequency Ablation and the control. The interval gives the range of effects that remain compatible with the data.

Plasma B-type Natriuretic Peptide (BNP) at 6 Months

• 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:
  • Radiofrequency Ablation: mean 2,354 versus 1,931 on control; difference 423.00 (95% CI -978.84 to 1,825), standardized effect d = 0.19; z-test p = 0.554.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Radiofrequency Ablation and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add measurements of BNP at baseline, at 6 months, and as a change measure. Their estimates do not form a uniformly clear pattern of differences between groups: the change comparison is in one direction, while the baseline and 6-month comparisons are in the other. The intervals for these comparisons are broad and include zero. Taken together, they do not provide a precise or consistent signal that resolves the uncertainty in the primary comparison.

These endpoints relate to the primary result by measuring a different aspect of the study’s stated clinical context. Ejection fraction is the MRI-based measure of cardiac function selected as the primary endpoint, while BNP is a plasma measure. A secondary biomarker can complement the primary outcome, but it is not an interchangeable measurement of the same construct. Agreement or disagreement between different measures can reflect differences in what they capture, in their measurement variability, or in the uncertainty of the estimates. The registry does not report an analysis explaining any relationship between BNP and ejection fraction.

The secondary results carry less weight than a prespecified primary analysis because multiple outcomes create more opportunities for apparently notable results to arise by chance. In general, looking at many endpoints without accounting for multiplicity can make unadjusted p-values look more persuasive than they are. The registry lists no reported analyses and does not describe a multiplicity adjustment or hierarchy among the secondary outcomes. These results are therefore best read as exploratory supporting information, not as independent confirmation of the primary finding.

The secondary comparisons are also based on outcome-specific analysis counts, and the counts differ for the change measure. Such differences make it important to consider which participants contributed to each result. The registry does not report missing-data methods or analyses that test the sensitivity of the secondary findings to unavailable observations. These limitations, together with broad intervals and multiple outcomes, leave the secondary evidence uncertain.

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

• Plasma B-type Natriuretic Peptide (BNP)
• Plasma B-type Natriuretic Peptide (BNP) at Baseline
• Plasma B-type Natriuretic Peptide (BNP) at 6 Months

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numerical measurement of change in ejection fraction. For a continuous outcome, a group mean describes the average observed value, while a standard deviation describes how dispersed individual observations are around that mean. The reported endpoint values are mean changes, not percentages of participants who improved. A mean can be influenced by particularly large or small observations, so the standard deviation and confidence interval are useful companions to the average.

What does a mean difference represent?

The mean difference compares the average change in the radiofrequency-ablation group with the average change in the medical-therapy group. For the primary endpoint, the estimate is 1.7. A positive estimate means the reported mean change was numerically larger in the ablation group under the stated comparison order. It does not describe how many individual participants had a larger change, and it does not indicate that every participant changed in the same direction.

The comparison is unadjusted, meaning it is derived directly from group summaries rather than from a model that accounts for other variables. Unadjusted comparisons can be useful for understanding the posted summary data. They may not match an analysis that adjusts for baseline values, stratification variables, or other prespecified factors. Whether the trial planned such adjustments is not reported in the registry record, and the registry lists no reported analyses.

How should the p-value be read?

The unadjusted p-value for the primary mean difference is 0.569. In general, a p-value describes the compatibility of the observed data with a statistical model that assumes no group difference, under the model’s assumptions. It is not the probability that the no-difference model is true, and it does not measure the clinical importance of the estimate. A value such as this does not prove no difference; it indicates that the observed summary alone does not provide a clear statistical distinction from zero under the unadjusted comparison.

Statistical significance and practical importance are separate questions. The size and precision of the estimate, the relevance of the outcome, the study design, and the completeness of measurement all matter. A p-value does not convey the full range of differences compatible with the data, so it should be interpreted alongside the confidence interval.

Why does the confidence interval matter?

A confidence interval describes a range of values that are reasonably compatible with the data and the method used to calculate the interval. The primary interval runs from -4.153 to 7.553. Because it includes zero, the data are compatible with no mean difference as well as with differences in either direction. Its breadth also shows that the estimate is not highly precise. The interval is not a guarantee that the true value lies within its limits, nor does it assign probabilities to individual values after the data have been observed.

What does variation tell us?

The standard deviation reflects variation among observed participant-level changes. The primary group standard deviations are 6.8 and 11.1. Larger variability makes it harder to estimate a group mean difference precisely when the number of observations is limited. This is one reason that a modest point estimate can be accompanied by a wide interval. The reported standard deviations describe the observed data; they do not tell whether the variation arose from measurement differences, clinical diversity, or other causes.

In general, over-dispersion means that data vary more than a chosen statistical model expects. It can make standard errors and confidence intervals too small if the model fails to account for that extra variation. The primary outcome is reported as a continuous measure with means and standard deviations; the registry does not report an over-dispersion assessment or a model used to address it. The term is a general statistical consideration, not a finding reported for this trial.

What is the role of randomization?

Random assignment is intended to make the groups comparable on average at the start of a trial, including on factors that are measured and factors that are not measured. It does not guarantee that groups will be identical, especially in a study with relatively few participants. The registry identifies the allocation as randomized, but details of sequence generation, concealment, and any stratification are not reported in the registry record. These details can affect how confidently the randomization process can be assessed.

Masking is listed as none. In general, lack of masking can influence care, participant behavior, outcome assessment, or decisions about whether measurements are obtained. MRI-based ejection fraction is an objective measurement, but the registry does not describe who interpreted the scans or whether assessors were unaware of group assignment. That information is not reported in the registry record.

What do the outcome counts mean?

For the primary endpoint, 19 participants were analyzed in each group. The registry notes that some outcomes could not be measured because a participant did not tolerate MRI or dropped out. The number enrolled was 41, so the endpoint analysis does not include every enrolled participant. For the BNP change endpoint, the group counts are 18 and 20. The registry does not report an imputation method, a missing-data model, or a sensitivity analysis assessing whether missing observations might change the results.

In general, missing-data methods rely on assumptions about why measurements are unavailable and how missing participants might have differed from those observed. If missingness is related to health status or treatment experience, a complete-case comparison may not represent all randomized participants. The registry does not provide enough detail to evaluate those assumptions for this trial. This uncertainty is distinct from the statistical uncertainty captured by the confidence interval, which quantifies sampling variability under its calculation method.

11. Confidence Intervals and Precision

The primary mean difference is 1.7, and its 95% confidence interval extends from -4.153 to 7.553. The interval includes zero and spans values indicating a difference in either direction. This means the estimated difference is not precise enough to determine the direction of the comparative change from these data alone. The interval’s breadth should be considered alongside the small analysis counts and the observed standard deviations of 6.8 and 11.1.

A confidence interval is an uncertainty range generated by a statistical method. In general, a 95% confidence procedure would cover the underlying parameter in 95% of repeated samples if its assumptions held. It is not a range containing 95% of individual participant outcomes, and it does not mean there is a 95% probability that the true difference is inside this particular interval. The primary interval describes uncertainty about the group mean difference, not the range of individual changes.

The BNP comparisons also have broad intervals. For the change measure, the mean difference is -281.0, with an interval from -991.0 to 429.0. For BNP at baseline, the difference is 704.0, with an interval from -524.8 to 1933.0. For BNP at 6 months, the difference is 423.0, with an interval from -978.8 to 1825.0. Each of these intervals includes zero, and each permits values in both directions. BNP measurements also have large reported standard deviations, contributing to uncertainty in these mean comparisons.

The intervals are unadjusted recalculations from the posted summary statistics. The registry lists no reported analyses, and no adjusted confidence intervals are reported. Confidence intervals do not address all sources of uncertainty: they do not correct for missing outcomes, unclear analysis choices, or the examination of multiple endpoints. Precision is therefore only one part of the evidence assessment.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, because the outcomes in this trial are continuous measures and the stated planning method reports participant counts per arm for such outcomes. The figures are illustrations based on the observed effect, not the trial’s original design assumptions. The planning assumptions 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 own sample-size assumptions are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm that the planning calculation would require to have an 80% chance of detecting the specified effect under its assumptions. The 90% power column gives the corresponding number for a 90% chance. Power is a property of a proposed design under assumed conditions; it is not a measure of whether the observed result is correct or important. These planning figures are not observed power.

The rows planning for 100%, 75%, and 50% of the observed effect illustrate how the assumed effect size changes the required enrollment. Smaller effects need more participants to distinguish them from random variation with the same target power and significance level. For example, the primary endpoint planning figures for 100% of the observed effect are 461 participants per arm for 80% power and 617 participants per arm for 90% power. Under planning for 50% of the observed effect, the corresponding figures are 1,841 and 2,465 participants per arm. These are planning illustrations rather than a reconstruction of the design chosen for the completed trial.

The curve follows the same general relationship between the assumed effect and the required sample size. It should be read as a planning aid: it does not show actual enrollment or actual probability that the trial detected an effect. A calculation based on the observed effect can be especially sensitive to how precisely that effect was estimated in a small study. It should not be treated as a recommendation for a future trial without a separate design assessment.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 1.700; pooled standard deviation σ = 9.205.
2. n = 2 × (1.96 + 0.842)² × 9.205² / 1.700² = 460.2, rounded up to 461 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
delta <- 1.7                      # observed difference in means
sigma <- 9.20461840599598                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(292162)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 461 (80% power), 617 (90% power)
 75% of observed effect: n per arm = 819 (80% power), 1,096 (90% power)
 50% of observed effect: n per arm = 1,841 (80% power), 2,465 (90% power)
power.t.test: 461.2 
Simulated power at n = 461 per arm: 0.798 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 lists the primary MRI-based ejection-fraction change and three BNP outcomes. It does not report a prespecified hierarchy for testing outcomes, a familywise error strategy, or another multiplicity adjustment. No analyses are listed as reported analyses. It is therefore not possible to determine from the registry record whether the posted outcome comparisons were selected from a larger set of planned analyses or how the investigators intended to interpret multiple tests.

Multiplicity matters because each additional statistical test creates another opportunity to observe a result that appears unusual through chance alone. Unadjusted p-values can be useful descriptive summaries, but when several outcomes are tested, they do not automatically preserve the same overall false-positive rate as a single planned test. The secondary BNP results should be interpreted with this context in mind. The registry does not state whether their analyses were intended to be confirmatory or exploratory.

The primary endpoint analysis includes 19 participants in each group, while the total enrollment is 41. The registry explains generally that outcomes could be unavailable because a participant did not tolerate MRI or dropped out. It does not identify which participants lacked a primary measurement, give reasons for each missing measurement, or report how missing observations were handled. The BNP change analysis has 18 participants in medical therapy and 20 in ablation; baseline and 6-month BNP counts are 19 in each group. The record does not explain the differences in these counts.

Whether analyses followed an intention-to-treat population, a per-protocol population, or another definition is not reported in the registry record. Details of imputation, sensitivity analyses, and assumptions about the missing observations are also not reported in the registry record. These omissions limit assessment of whether the results could be affected by outcome availability or analysis choices.

The protocol’s statistical analysis plan, including any interim analyses, is not reported in the registry record. Consequently, the registry does not establish which analyses were planned before results were known, whether any interim monitoring occurred, or whether the displayed comparisons match the planned primary analysis. These are reporting limitations; they do not by themselves establish that the analyses were inappropriate.

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 0% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: cardiac tamponade (9.1%), stroke (4.5%), heart failure hospitalisation (4.5%).

The adverse-event record lists 19 participants at risk in the medical-therapy group and 22 in the radiofrequency-ablation group. It records zero serious adverse events for medical therapy and 4 for ablation. It lists zero other adverse events in both groups. These are the registry’s recorded counts; they should be read with the group-specific denominators and not treated as a complete description of every possible safety outcome.

The record also lists cardiac tamponade at 9.1%, stroke at 4.5%, and heart failure hospitalisation at 4.5% among the top serious-event terms. The registry does not provide further event-level detail in the posted information, so the terms and percentages should not be used to infer additional information about timing, severity beyond the serious classification, or causality. Death counts are not reported in the registry record.

The safety group counts do not match the primary endpoint analysis counts, and the reason for the difference is not reported in the registry record. Adverse-event counts and outcome analysis counts serve different purposes and have different denominators. With the small recorded groups and limited detail, these figures describe the posted safety record but do not settle comparative safety.

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

The posted primary result is a mean difference of 1.7 in change in MRI-measured ejection fraction, favoring a numerically larger mean change in the radiofrequency-ablation group. Its 95% confidence interval, from -4.153 to 7.553, includes zero and allows differences in either direction. The result is therefore uncertain about both the direction and the size of the comparative change. The unadjusted p-value of 0.569 is consistent with that uncertainty; it is not proof of no difference.

The result does not show that the two treatments are equivalent. Equivalence requires a specifically designed analysis with a prespecified range of differences considered unimportant, and such a margin or analysis is not reported in the registry record. Nor does the result establish that either treatment caused an improvement in every participant. A group mean summarizes observed changes, and participant-level responses can vary substantially around that average.

The endpoint is a measure of cardiac function, not a complete measure of clinical benefit or harm. The primary result does not answer every question about symptoms, hospital use, survival, or safety. BNP outcomes provide additional measurements but have broad intervals and are subject to the limitations of multiple secondary comparisons and missing outcome information. The safety record lists serious events, but the available counts do not provide a complete comparative safety assessment.

The registry identifies the trial as randomized, which is a design feature intended to support a fair comparison, but the record does not report key details of the randomization process or the statistical plan. The primary analysis includes fewer participants than the enrollment count, and the record gives only general reasons why some outcomes were unavailable. These features add uncertainty beyond the confidence interval itself.

The most defensible reading is that the posted data offer an imprecise estimate of the difference in mean ejection-fraction change between the groups. They neither establish a clear difference nor establish sameness. The findings should be understood as the results available for this trial’s measured outcomes, with the limits of the analysis counts, reporting detail, and precision kept in view.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between a point estimate and the certainty of that estimate. The primary mean difference is positive, but its interval extends on both sides of zero. Reading only the point estimate could give an overly definite impression; reading only the p-value could incorrectly suggest that no difference exists. Together, the estimate and interval show that the data leave substantial uncertainty about the comparative change.

The study also shows why outcome variability matters. The primary group standard deviations are large in relation to the mean changes, and the analysis counts are 19 participants per group. A trial with limited observations and variable measurements will generally estimate a mean difference less precisely than a larger study with less variability. This is reflected in the breadth of the reported interval, not merely in the p-value.

Another statistical lesson is the importance of separating trial results from planning illustrations. The sample-size figures use observed effects and stated planning assumptions; they do not reveal the original design rationale and are not observed power. The registry record does not report the original sample-size justification, analysis plan, or multiplicity strategy. A careful reader should distinguish these missing design details from the post hoc planning calculations.

Finally, the record highlights how outcome-specific missingness and changing analysis counts affect interpretation. Enrollment does not mean every participant contributed to every endpoint. Knowing who was analyzed, why observations were unavailable, and how missing data were handled is important when assessing whether a comparison represents the randomized groups. These details are not fully reported in the registry record, so the statistical findings must be read as informative but limited estimates.

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 endpoint is available for 19 participants in each group, whereas enrollment was 41. The registry notes that MRI could not be tolerated by some participants or that some dropped out, but it does not identify the number or group assignment of participants affected by each reason. Without that detail, it is difficult to assess whether the missing endpoint measurements were balanced or related to participants’ outcomes.

The adverse-event denominators differ from the primary endpoint analysis counts: the record lists 19 at risk for medical therapy and 22 for ablation. The registry does not explain the relationship between those safety counts and the outcome analysis population. The serious-event counts and terms therefore have to be interpreted according to their recorded denominators, without assuming that they describe precisely the same participants as the primary analysis.

The registry reports no sponsor analyses, no statistical analysis plan, and no detailed model specification. The comparisons are unadjusted recalculations from summary statistics. It is not reported whether the original analysis was intended to adjust for baseline ejection fraction, use another method, or address multiple endpoints in a particular way. The absence of those details limits comparison between the posted summaries and the planned inferential approach.

The record does not describe random-sequence generation, allocation concealment, site organization, MRI assessment procedures, or masking of outcome assessors. These details are not reported in the registry record, so the possible influence of those design and measurement features cannot be assessed from the posted information.

The BNP measures have large standard deviations and broad intervals, and the registry does not report analyses addressing multiplicity or missing-data sensitivity. The trial’s completed status does not resolve these reporting gaps. These limitations do not negate the observed data, but they constrain how firmly the estimates can be interpreted or generalized beyond the specific study population and measurements.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Curing Atrial Fibrillation in Heart Failure — NCT00292162.
• Registry record last updated 2012-06-01; status last verified 2012-05.
• Results first posted 2012-06-01.
• 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, unmasked, parallel-group trial of radiofrequency ablation versus medical therapy for atrial fibrillation in people with chronic heart failure. Enrollment was 41. The primary endpoint was change in MRI-measured left ventricular ejection fraction from baseline to 6 months.

The primary analysis included 19 participants per group. The unadjusted mean difference was 1.7, with a 95% confidence interval from -4.153 to 7.553 and an unadjusted p-value of 0.569. The interval includes zero and is broad, so the comparative estimate is imprecise. BNP outcomes were also posted, with broad intervals. The safety record lists 4 serious adverse events in the ablation group and none in medical therapy; death counts are not reported in the registry record.

The registry does not report the original sample-size rationale, the statistical analysis plan, missing-data methods, or multiplicity procedures. Outcome-specific counts differ, and the reasons for unavailable measurements are reported only generally. The posted estimates should be read in light of those limitations.