Renal Nerve Denervation in Patients With Hypertension and Paroxysmal and Persistent Atrial Fibrillation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Renal Nerve Denervation in Patients With Hypertension and Paroxysmal and Persistent Atrial Fibrillation (NCT02064764), a randomized na study. The primary outcome is Proportion of Subjects in Each Arm That Experience Safety Composite Events.

2. Clinical Question

The registry also describes effectiveness as freedom from chronic treatment failure through a minimum of six months of follow-up. That measure is listed among secondary outcomes rather than as the posted primary endpoint. The central statistical question is therefore about the observed safety-event counts and how much uncertainty surrounds the between-arm comparison, not whether either procedure should be chosen in clinical practice.

3. Trial Design

This was a randomized, parallel-group study with no masking. The registry lists an enrollment of 102 and marks the study completed. The primary completion date is 2021-04-19. The two arms were pulmonary vein isolation alone and pulmonary vein isolation combined with renal nerve denervation. The registry identifies Medtronic Vascular as the sponsor.

The posted primary endpoint is the count of participants in each arm who experienced events in a safety composite. The registry describes the composite as including end stage renal disease, death, significant embolic event, renal artery perforation or dissection requiring intervention, vascular complications, hospitalization for hypertensive crisis, new renal artery stenosis, cardiac damage, pulmonary vein stenosis, atrio-esophageal fistula, arrhythmia, and persistent phrenic nerve palsy. The observation period depends on the event, with follow-up up to one or six months after the procedure.

The posted primary-arm counts are based on 36 participants in the cryoablation-only arm and 34 in the combined-treatment arm. Those analyzed group sizes do not sum to the registry’s enrollment figure, and the reasons for that difference are not reported in the registry record. The record does not provide detailed eligibility criteria, the randomization procedure, allocation concealment, or the statistical plan used to determine the original sample size. It also does not report why masking was absent, although the study is explicitly recorded as having none.

Several other outcomes are listed, including blood pressure, heart rate, symptoms, chronic treatment success off specified anti-arrhythmic drugs, procedural measures, and atrial-fibrillation burden. Results are posted for only some of these outcomes in the available record. The number of posted secondary outcomes is six, while ten outcome measures and two analyses are recorded overall. The timing and analysis details for every measure are not fully described.

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: 28 subjects were exited prior to randomization for not meeting study eligibility criteria. Of the 74 randomized subjects, 3 in the PVI+RDN group were not treated and 1 in the Control group (PVI only) were not treated.

Overall 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 Proportion of Subjects in Each Arm That Experience Safety Composite Events, measured over Up to one or six months post procedure depending on the event.

The primary endpoint counts participants in each arm who experienced at least one event included in a safety composite. Its purpose is to describe the occurrence of a broad range of potential harms rather than to focus on a single complication. The listed components span renal, vascular, embolic, cardiac, and rhythm-related events. Because each component can have a different clinical character and timing, a composite can summarize whether any listed event occurred while obscuring which component accounts for the observed count.

The registry defines the comparison as both the event rate within each arm and the difference between arms. The posted counts are 1 participant among 36 in the cryoablation-only arm and 3 among 34 in the combined-treatment arm. The recalculated risk-difference confidence interval extends from -0.049 to 0.170; the upper endpoint is reported as given, despite the general limit on displayed decimal places. To avoid overstating precision, the interval is best read qualitatively: it includes zero and spans values on either side of no difference.

The event-specific window is up to one or six months after the procedure, depending on the component. This matters because the endpoint does not represent one uniform observation period for every event. The registry record does not report a component-by-component breakdown of the primary composite counts or details on how repeat events were handled. The composite therefore provides a broad safety summary, but the posted total alone cannot show the type, timing, or recurrence of events that contributed to it.

7. Results Posted in the Registry

• Cryoablation and Renal Nerve Denervation: 8.8% (3/34) versus 2.8% (1/36) on control; risk difference 6.0 percentage points (95% CI -4.9 to 17.0), risk ratio 3.18 (0.35–29.07); unadjusted two-proportion z-test p = 0.276.

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.

Difference in Heart Rate at 6 Months and 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:
  • Cryoablation and Renal Nerve Denervation: mean 1.80 versus -1.90 on control; difference 3.70 (95% CI -4.22 to 11.62), standardized effect d = 0.22; z-test p = 0.360.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cryoablation and Renal Nerve Denervation and the control. The interval gives the range of effects that remain compatible with the data.

Percent of Time in AF Burden Over All Follow-up Occurring After the Blanking Period

• 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:
  • Cryoablation and Renal Nerve Denervation: mean 1.75 versus 2.78 on control; difference -1.03 (95% CI -3.68 to 1.62), standardized effect d = -0.18; z-test p = 0.446.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cryoablation and Renal Nerve Denervation and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results add descriptive information about heart rate and atrial-fibrillation burden, while other listed outcomes include blood pressure, symptoms, procedural measures, and chronic treatment success. The record does not post results for every listed secondary outcome. Across the two available continuous comparisons, the uncertainty intervals include zero, so neither provides a precise between-arm difference. These results do not resolve the uncertainty in the primary safety comparison.

Secondary outcomes can help describe different aspects of a trial, but they do not substitute for the primary endpoint. The primary result concerns a composite of safety events; heart-rate change and atrial-fibrillation burden measure different constructs and use different scales. A pattern across outcomes can be informative descriptively, but it should not be treated as a single confirmatory conclusion when the outcomes are distinct and the registry does not report a prespecified hierarchy or analysis plan.

Unadjusted secondary results carry less weight because testing several outcomes creates more opportunities for chance findings. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a plan specifying which secondary outcomes were confirmatory. It also does not report results for all of the listed outcomes. Without those details, isolated secondary findings should be treated as exploratory or descriptive rather than as independent proof of an effect.

The overall pattern is one of limited precision rather than a consistent, definitive separation between arms. That observation does not establish that outcomes are the same; it reflects the uncertainty in the posted comparisons and the incomplete outcome reporting. Interpretation should remain tied to each outcome’s definition, analysis, and follow-up period.

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

• Change in Office Systolic and Diastolic Blood Pressure at 6 Months From Baseline
• Difference in Heart Rate at 6 Months and Baseline
• Procedural Measures
• Proportion of Participants With Symptoms at 6 Months Between Study Arms
• Rate of Chronic Treatment Success (Primary Effectiveness Endpoint) for Subjects Off of Class I and III Anti-arrhythmic Drugs Following the Blanking Period.
• Percent of Time in AF Burden Over All Follow-up Occurring After the Blanking Period

9. Statistical Interpretation

10. Statistical Methods Explained

The registry record gives a primary endpoint based on event counts and reports a log-rank analysis. The recalculated comparison uses the posted participant counts to estimate an unadjusted risk difference and confidence interval. These approaches answer related but not identical questions, so their results should be interpreted according to the method that produced them.

What does a risk difference describe?

A risk difference compares the proportion of participants with an event in one arm with the proportion in the other. It is expressed on the probability scale: zero represents no difference, and values on opposite sides of zero indicate different directions of the contrast. For this trial, the reference arm is cryoablation only and the comparison arm adds renal nerve denervation. The posted counts are 1 of 36 and 3 of 34, respectively. The recalculated estimate uses these group summaries without adjustment for other factors.

An unadjusted estimate is transparent and can be calculated from the reported counts, but it does not account for prognostic factors, differences in follow-up, or other design features beyond the summarized data. The registry record does not report an adjusted effect estimate for this comparison. With few events, the estimate is especially sensitive to the experience of individual participants, and uncertainty is substantial.

What does a confidence interval add?

A confidence interval gives a range of effect values compatible with the data under the calculation method and its assumptions. It is not a guarantee that the true effect lies in the interval, nor does it describe the range of individual participant outcomes. For the primary risk difference, the interval includes zero. That means the data do not distinguish a nonzero difference from no difference with precision. The interval also extends to values on both sides of zero, so its direction is uncertain.

The confidence interval is more informative than a significance label alone because it shows the range of plausible estimates, not just whether a threshold was crossed. Here, the interval’s width reflects limited precision. It should not be read as proof that all values within it are equally likely or as evidence that clinically important effects have been ruled out.

Why is a log-rank test reported?

A log-rank test is commonly used to compare time-to-event patterns between groups. It uses information about when events occur and can account for participants whose follow-up ends before an event is observed, under the method’s assumptions. The registry reports a log-rank p-value of 0.28, but it does not post a corresponding sponsor estimate or confidence interval for that analysis. The record also does not give enough detail to reconstruct the time-to-event dataset, censoring pattern, or model specification.

The recalculated p-value of 0.276 is based on a simple unadjusted comparison of the posted summary statistics. It is not a replacement for the sponsor’s analysis and should not be treated as if it replicated the log-rank calculation. A difference between methods can arise because they use different information or assumptions; the registry record does not explain the precise relationship between the reported analysis and the count-based summary.

How should p-values be understood?

A p-value evaluates the observed data against a model that assumes no difference, together with the assumptions of the test. It does not quantify the size or importance of an effect, and it cannot by itself establish equivalence. A large p-value can occur when the true difference is small, when data are sparse, or when uncertainty is broad. The primary comparison has few events, so the p-value should be read alongside the interval and counts rather than as a standalone conclusion.

For continuous secondary outcomes, the recalculated comparisons use group means and standard deviations to estimate mean differences. A pooled standard deviation provides a common scale for describing variability across the two arms; standardized effect values are also calculated from the posted summaries. The registry record does not report adjustment for baseline values or other covariates in these recalculations. Normal approximations are used for the planning illustrations, not to claim that every outcome follows a normal distribution.

Why can over-dispersion matter?

For count outcomes, over-dispersion means that observed variation exceeds what a simple count model would expect. If it is present but ignored, standard errors may be too small and confidence intervals too narrow. The registry record does not report a model-based over-dispersion assessment for the primary endpoint. The posted count-based re-calculation does not establish that a particular count model was used by the sponsor.

In general, statistical methods need to match outcome type and follow-up structure. A binary event summary, a time-to-event analysis, and a continuous mean comparison retain different information. The record does not report enough detail to evaluate all assumptions, missing-data procedures, or analysis-population definitions for the sponsor’s analyses.

11. Confidence Intervals and Precision

Precision is limited for the primary comparison. The observed event counts are 1 participant in the cryoablation-only arm and 3 in the combined-treatment arm, with 36 and 34 participants in those arms. A small number of events provides limited information about the underlying event risks, so the estimated contrast is uncertain. The recalculated confidence interval includes zero and extends to values in either direction. It therefore does not support a precise conclusion about which arm has the higher risk.

The registry-reported log-rank p-value is 0.28. The recalculated unadjusted p-value is 0.276. Neither number conveys the range of effect sizes compatible with the data; that is the role of the confidence interval. The record does not provide a sponsor confidence interval for the log-rank analysis, so its precision cannot be assessed from the reported p-value alone.

The continuous secondary comparisons also have intervals that cross zero. For heart-rate change, the mean difference is 3.7 beats per minute, with a confidence interval from -4.218 to 11.62. For atrial-fibrillation burden, the mean difference is -1.03 percentage points of time, with a confidence interval from -3.68 to 1.62. These ranges include no mean difference and allow values on both sides of it. The data therefore do not pin down the direction or size of either comparison with high precision.

Confidence intervals concern uncertainty in group-level estimates, not the range of outcomes that an individual might experience. Their interpretation also depends on the calculation method and assumptions. The registry record does not report enough information to assess all aspects of follow-up, missingness, or the sponsor’s interval construction. The intervals should be read as uncertainty summaries, not as guarantees or as proof that effects outside the limits are impossible.

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 illustrations based on the observed effect, not the trial’s original design. For these binary and continuous comparisons, the displayed figures represent participants per arm. They are not total event counts. The stated 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 to the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the planned number of participants per arm under those assumptions for a hypothetical study that has an 80% chance of detecting the specified effect if that effect is the true one. The 90% power column describes the corresponding planning target for a 90% chance. These are prospective design calculations, not evidence about what the completed trial could detect. This is not observed power.

Each row uses a different fraction of the observed effect as the target. Planning for 75% of the observed effect or 50% of the observed effect means trying to detect a smaller difference than planning for 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants under the stated assumptions. The listed sample sizes can therefore rise substantially as the target effect is reduced.

These illustrations should not be treated as a recommended design for a future study. They rely on the observed effect, which may itself be uncertain, and on simplifying assumptions about allocation, significance level, and the approximation used. The registry record does not report the assumptions that informed the actual enrollment target, nor does it establish that the planning illustrations account for attrition, multiple testing, or the time-to-event analysis.

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 = 0.028; treatment proportion p₁ = 0.088; average p̄ = 0.058.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3306 = 0.6479.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3278 = 0.2759.
4. n = (0.6479 + 0.2759)² / (0.0605)² = 233.5, rounded up to 234 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 <- 0.0277777777777778                          # control proportion
p1 <- 0.0882352941176471                          # 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(2064764)
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 = 234 (80% power), 313 (90% power)
 75% of observed effect: n per arm = 365 (80% power), 488 (90% power)
 50% of observed effect: n per arm = 705 (80% power), 943 (90% power)
power.prop.test: 233.5 
Simulated power at n = 234 per arm: 0.820 (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

The registry reports a sponsor analysis using a log-rank method, with p = 0.28. The recalculated unadjusted comparison from the posted primary counts has p = 0.276. The values are close, but the recalculation is not a reproduction of the sponsor’s analysis: the log-rank test uses event-time information, while the recalculation uses the posted summary counts. The record does not provide the sponsor’s effect estimate or confidence interval for the log-rank analysis.

The recalculated risk difference and its interval are useful for describing the contrast on an absolute scale, but they do not replace the sponsor’s stated analysis. The registry record does not report a discrepancy between the posted analysis and the recalculation. Where an analysis differs, the sponsor’s own analysis takes precedence; in this case, the two reported p-values are close, while the methods and available outputs remain distinct.

Neither p-value establishes that the arms are equivalent or that there is no meaningful difference. The event counts are small, and the recalculated interval spans values on either side of zero. Interpretation should therefore give priority to the endpoint definition, event counts, method, and uncertainty together, rather than relying on a p-value alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes in addition to the primary safety composite. When many outcomes are examined, the chance of at least one apparently unusual result can increase even if no true differences exist. Statistical procedures can control this risk, or an analysis plan can specify a hierarchy of outcomes and tests. The registry record does not report whether multiplicity was addressed, whether a hierarchy was prespecified, or whether the reported secondary analyses were confirmatory.

The record also does not report how missing outcome data were handled, how many participants contributed to each secondary analysis, or whether the analyses used an intention-to-treat or another defined population. The posted primary arm sizes are 36 and 34, but the reason they differ from the enrolled total is not reported in the registry record. The effect of withdrawals, unavailable measurements, or exclusions cannot therefore be evaluated from the posted summary alone.

For a time-to-event method, interpretation depends on event timing and on how participants without an observed event contribute through censoring. The registry gives a log-rank p-value but does not report the censoring details, event-time data, or analysis population. For the count-based re-calculation, only group-level counts and denominators are available, which limits assessment of follow-up completeness and event handling.

These omissions matter because missingness and selective outcome reporting can affect both the estimate and its uncertainty. If participants with unavailable outcomes differ from those measured, complete-case results may not represent the randomized groups. This is a general concern, not evidence that such bias occurred in this trial. The registry record does not provide enough information to determine whether missing data were present or to assess the methods used to address them.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: atrial fibrillation (26.5%), atrial flutter (14.7%), acute myocardial infarction (5.9%), cerebrovascular accident (5.9%), ventricular extrasystoles (5.6%).

The adverse-event summary lists serious adverse events affecting 17 of 36 participants in the cryoablation-only arm and 20 of 34 in the combined-treatment arm. Other adverse events affected 22 of 36 and 24 of 34 participants, respectively. The record lists 1 death in the cryoablation-only arm and 0 in the combined-treatment arm. These are descriptive counts and should not be read as adjusted comparisons or as proof of causation.

The listed serious-event terms include atrial fibrillation at 26.5%, atrial flutter at 14.7%, acute myocardial infarction at 5.9%, cerebrovascular accident at 5.9%, ventricular extrasystoles at 5.6%, and anaemia at 2.9%. The registry record does not explain the denominator used for each term or whether participants could contribute to more than one term. These percentages should therefore be interpreted as the registry’s reported summaries, not as directly comparable risks for each arm.

Serious adverse events and the primary safety composite are not interchangeable summaries. The record does not report which serious adverse events contributed to the primary endpoint or provide enough detail to determine overlap among events. Differences in the posted counts alone do not establish that one approach caused more or fewer events.

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

The posted results describe a randomized comparison of pulmonary vein isolation alone with pulmonary vein isolation plus renal nerve denervation in participants with hypertension and paroxysmal or persistent atrial fibrillation. For the primary safety composite, the registry lists 1 affected participant in the cryoablation-only arm and 3 in the combined-treatment arm. The recalculated interval includes zero and spans values in either direction. This means that the available summary does not establish a clear difference, while also leaving substantial uncertainty about the size and direction of any difference.

The findings do not demonstrate equivalence. Equivalence requires a prespecified margin and an analysis designed to show that the difference is sufficiently small; the registry record does not report such a margin or design. Nor does the absence of a statistically clear result prove that no difference exists. Sparse events and broad uncertainty can make it difficult to distinguish effects from random variation.

The secondary results are also uncertain and cover distinct outcomes. They cannot be combined into a general conclusion about effectiveness, especially because the record does not report results for all listed outcomes or a multiplicity plan. A result for a physiological measure or rhythm burden would not by itself establish a difference in the primary safety composite or in chronic treatment success.

The registry describes the study as evaluating feasibility and characterizing safety and effectiveness. The posted summaries can inform how the observed data compare, but they do not provide every detail needed to assess implementation, missing data, or analysis assumptions. These statistical results are not medical advice and should not be interpreted as a recommendation for or against either procedure.

18. Why This Trial Matters Statistically

This trial illustrates why clinical comparisons should be read through both effect estimates and uncertainty. The primary outcome is a composite safety measure, and its observed counts are small. A p-value alone would conceal how imprecisely the between-arm contrast is estimated; the interval makes clear that the data remain compatible with effects in either direction. This is an important distinction between not finding a clear difference and demonstrating that differences are absent.

The design also raises a general interpretive issue: a composite combines events that may differ in severity, frequency, and timing. The composite can offer a broad summary, but without component-level results readers cannot identify which events drove the count. The event-specific observation windows, which vary by component, further matter when interpreting the aggregate endpoint.

The comparison between a sponsor-reported log-rank test and a count-based recalculation demonstrates that analysis methods use different information. A time-to-event approach can account for event timing, while a simple count comparison focuses on whether an event was recorded in each group. These are related perspectives, not interchangeable results.

Finally, planning illustrations based on observed effects are not evidence of the trial’s original design adequacy or of its observed power. Their assumptions must be distinguished from the registry’s actual design information, which is not reported in full. Together, these points show why transparent reporting of populations, missing data, analysis plans, and component outcomes is essential for judging the strength of clinical evidence.

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.

The primary comparison has few observed composite events, which limits precision. The registry provides a broad composite but does not post component-specific primary counts, so the event types contributing to the comparison cannot be identified. The components also have different stated observation windows, up to one or six months after the procedure, rather than one common window for every event.

The registry’s enrollment is 102, while the posted primary analysis groups contain 36 and 34 participants. The record does not explain the difference or state whether the posted denominators represent all randomized participants, participants treated, or another analysis population. Reasons for any exclusions, losses to follow-up, or missing outcome data are not reported in the registry record.

The sponsor’s primary analysis is reported as a log-rank p-value without an accompanying effect estimate or confidence interval. The registry does not provide the time-to-event data, censoring details, or sufficient analysis specifications to evaluate that result fully. The recalculated risk difference is based on aggregate counts and cannot account for event timing or covariates.

The record does not report the original sample-size justification, interim analyses, a full statistical analysis plan, multiplicity procedures, or a hierarchy for secondary outcomes. Results are not posted for every listed secondary endpoint. The trial is recorded as unmasked, and further information about allocation procedures is not reported in the registry record. These reporting limits restrict assessment of bias, generalizability, and the robustness of the analyses; they do not establish that a particular bias occurred.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Renal Nerve Denervation in Patients With Hypertension and Paroxysmal and Persistent Atrial Fibrillation — NCT02064764.
• Registry record last updated 2024-02-23; status last verified 2024-01.
• Results first posted 2024-02-23.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed, randomized, unmasked, parallel-group study sponsored by Medtronic Vascular. It enrolled 102 participants and compared pulmonary vein isolation alone with pulmonary vein isolation plus renal nerve denervation in a population with hypertension and paroxysmal or persistent atrial fibrillation.

The primary endpoint was the number of participants experiencing events in a safety composite, with event-specific follow-up up to one or six months after the procedure. The posted counts were 1 of 36 in the cryoablation-only arm and 3 of 34 in the combined-treatment arm. The registry reports a log-rank p-value of 0.28; the recalculated count-based comparison is imprecise and its confidence interval includes zero.

Some secondary results and adverse-event summaries are posted, but the registry record does not report results for every listed outcome or provide full details on missing data, analysis populations, multiplicity, or the original sample-size justification. The available results are descriptive and uncertain; they do not establish equivalence or a definitive between-arm difference.