Prevention of Syncope by Cardiac Pacing in Patients With Bifascicular Block: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Prevention of Syncope by Cardiac Pacing in Patients With Bifascicular Block (NCT01463358), a randomized na study. The primary outcome is Combined Endpoint Defined as First Occurrence Among the Following Events 1)Syncope Episode of Any Origin; 2)Presyncopal Episode With Documented Cardioinhibitory Origin 3) Atrioventricular Block of Any Degree Associated With Patient Symptoms.

2. Clinical Question

The study objective was to evaluate bradycardia pacing with respect to symptoms. The comparison is therefore not limited to syncope alone: the primary outcome also includes specified symptomatic presyncopal episodes and symptomatic atrioventricular block. This matters when interpreting the result, because a participant may meet the combined endpoint through any of its listed components.

The registry describes randomized allocation and a parallel-group design, with no masking. It reports outcome counts for DDI30 and DDD60 at the 2-year timeframe. It does not report participant-level clinical characteristics, the distribution of endpoint components, or details about how symptoms were elicited and adjudicated beyond the endpoint definitions. Those omissions limit how finely the results can be interpreted, even though the group comparison and primary endpoint count are posted.

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. The arms are DDI30, backup pacing only with a lower rate of 30 ppm, and DDD60, full pacing support with a lower rate of 60. The record lists a device intervention for each arm; its intervention listing uses the same device name for both, while the arm descriptions distinguish the pacing settings. The reported outcome groups are 49 participants for DDI30 and 52 for DDD60.

The registry records enrollment as 101 and trial status as completed. It identifies bifascicular block and syncope as the conditions under study. The stated objective is to evaluate bradycardia pacing with respect to symptoms in patients with bifascicular block and syncope of unexplained origin. The primary outcome timeframe is 2 years; both listed secondary outcomes also use a 2-year timeframe.

No masking means the registry does not describe participants or study staff as blinded to group assignment. In general, knowledge of assignment can affect care, reporting, or assessment of symptoms, although random allocation is intended to reduce systematic differences between groups at assignment. The record does not report procedures for endpoint adjudication or any other safeguards against assessment bias.

Details about the original sample-size justification, planned statistical methods, allocation concealment, trial protocol, participant flow, and analysis populations are not reported in the registry record. The posted sample-size illustrations are calculations based on observed effects, not evidence of the original design assumptions. The registry reports outcome counts and unadjusted comparisons, but does not list reported analyses for the secondary outcomes. These gaps should be kept in view when assessing the strength and scope of the posted results.

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

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 Combined Endpoint Defined as First Occurrence Among the Following Events 1)Syncope Episode of Any Origin; 2)Presyncopal Episode With Documented Cardioinhibitory Origin 3) Atrioventricular Block of Any Degree Associated With Patient Symptoms, measured over 2 years.

The primary endpoint is a combined binary outcome: whether a participant experienced at least one qualifying event during the 2-year timeframe. Its components are syncope of any origin; a presyncopal episode with documented cardioinhibitory origin; or atrioventricular block of any degree associated with patient symptoms. The registry description also refers to syncope episodes, symptomatic presyncopal episodes associated with a device intervention (ventricular pacing), and symptomatic episodes with documentation of intermittent or permanent atrioventricular block.

A combined endpoint can capture several clinically relevant event types in one participant-level measure. That approach may be useful when the research question concerns a broader pattern of symptoms and rhythm-related events rather than one event type alone. It also means the result does not reveal which component chiefly accounts for the group comparison. Component-specific primary outcome counts are not reported in the registry record.

The posted result is a count of participants experiencing an event, rather than a count of all episodes. Consequently, repeated events in one participant are not represented as multiple participants in this outcome measure. The combined endpoint is used to compare the frequency of participants reaching any listed component in the two pacing groups. Its breadth should be considered when interpreting it alongside the secondary outcome for first symptomatic syncope or presyncope independently of origin.

7. Results Posted in the Registry

• DDD60: 13.5% (7/52) versus 32.7% (16/49) on control; risk difference -19.2 percentage points (95% CI -35.3 to -3.1), risk ratio 0.41 (0.19–0.92); unadjusted two-proportion z-test p = 0.022.

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.

Occurrence of First Symptomatic Episode (Syncope or Pre-syncope), Independently From Origin.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • DDD60: 25.0% (13/52) versus 44.9% (22/49) on control; risk difference -19.9 percentage points (95% CI -38.1 to -1.7), risk ratio 0.56 (0.32–0.98); unadjusted two-proportion z-test p = 0.036.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for DDD60 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Atrial Fibrillation

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • DDD60: 34.6% (18/52) versus 18.4% (9/49) on control; risk difference 16.2 percentage points (95% CI -0.6 to 33.1), risk ratio 1.88 (0.94–3.79); unadjusted two-proportion z-test p = 0.065.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DDD60 and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary outcomes, the observed directions are mixed. The first symptomatic episode of syncope or presyncope, regardless of origin, has a lower posted event proportion in DDD60 than in DDI30, aligning directionally with the primary combined endpoint. Atrial fibrillation has a higher observed proportion in DDD60 than in DDI30. These outcomes address different event types, so their directions need not match.

The first symptomatic episode outcome is related to the primary endpoint because both include syncope or presyncope. They are not identical measures: the primary outcome also includes specified symptomatic atrioventricular block and requires particular criteria for presyncope, while the secondary outcome is defined as syncope or presyncope independently from origin. Atrial fibrillation is a separate outcome and does not form part of the primary endpoint definition.

The secondary results can help describe the broader pattern of recorded outcomes, but they do not independently establish or negate the primary comparison. Their relation to the primary result depends on the endpoint definitions, the number of outcomes examined, and the uncertainty around each estimate. In particular, a secondary result that differs in direction does not by itself explain the primary finding or identify a mechanism.

Unadjusted secondary comparisons carry less weight when several outcomes are examined because multiple testing increases the chance of at least one apparently notable result. The registry does not report a multiplicity adjustment, a prespecified hierarchy among outcomes, or reported analyses for the secondary endpoints. Without those details, these comparisons are best treated as supportive descriptive information rather than definitive evidence. The outcome-specific estimates and intervals are more informative than a simple tally of which comparisons appear statistically notable.

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

• Occurrence of First Symptomatic Episode (Syncope or Pre-syncope), Independently From Origin.
• Atrial Fibrillation

9. Statistical Interpretation

10. Statistical Methods Explained

What kind of outcome is being compared?

The primary measure is binary at the participant level: each participant is counted according to whether any qualifying event occurred within the 2-year timeframe. The posted group counts are 16 of 49 for DDI30 and 7 of 52 for DDD60. This format is different from a rate of recurrent episodes or a time-to-first-event estimate. The registry gives a count of participants with an event, and does not report event timing or a recurrent-event analysis.

Binary outcomes can be summarized as the proportion with an event in each group and as a contrast between those proportions. The posted comparison uses a risk difference, expressed as DDD60 minus DDI30. A negative value means the observed event proportion is lower in DDD60; a positive value would mean it is higher. The posted estimates are -0.192 for the primary outcome, with group proportions listed as 0.327 and 0.135, respectively. These are unadjusted results.

What does the confidence interval describe?

A confidence interval communicates uncertainty around an estimated contrast. In general, a wider interval indicates less precision, while a narrower interval indicates more precision, conditional on the method and assumptions used. For the primary risk difference, the posted interval extends from -0.353 to -0.031. Since zero represents no risk difference, an interval that does not include zero is consistent with a nonzero contrast under the interval procedure. The registry does not report the method used to calculate these intervals, so the exact statistical procedure should not be inferred.

Confidence intervals do not describe the range of individual participant outcomes, and they do not ensure that the true value is inside the reported limits. They are also not a substitute for considering design, endpoint definition, missingness, or multiplicity. The interval helps describe precision in the estimated group difference; it does not by itself establish the importance of that difference.

How should a p-value be read?

A p-value assesses how unusual results at least as incompatible with a specified null model would be if that model and the analysis assumptions held. The posted primary unadjusted p-value is 0.022. It is not the probability that the observed difference arose by chance, and it does not measure the size or importance of the effect. Statistical evidence and practical meaning are separate considerations.

The registry does not describe the test used for the posted p-values, nor does it provide a full statistical analysis plan. It also does not list adjusted analyses. Accordingly, the comparisons are best described as the unadjusted estimates posted in the registry, without attributing them to a particular model or test.

Why can over-dispersion matter?

Over-dispersion is a general issue for count models when variability in event counts exceeds what the chosen model expects. It can make standard errors too small if ignored. It is not directly the defining concern for the posted primary endpoint, which counts participants with any event rather than modeling each participant's number of episodes. The registry does not report a recurrent-event count model or an over-dispersion assessment. More generally, analysis choices should match the outcome structure: a participant-level binary measure, recurrent event counts, and time-to-event data answer different questions.

What can and cannot be inferred from randomization?

Random allocation is intended to make the assigned groups comparable at baseline on average, including with respect to characteristics that are not measured. This supports a fairer comparison than treatment selection based on participant characteristics. It does not guarantee that the groups are identical, and it does not address problems that may arise after allocation, such as missing outcomes, deviations from assignment, or differences in assessment.

The record identifies randomized allocation and a parallel design, but allocation concealment, adherence, participant flow, and the population included in each analysis are not reported in the registry record. No masking is described. These features matter because knowledge of treatment assignment can influence subjective symptom reporting or assessment. The record also does not report component-specific primary endpoint counts or details of event adjudication.

The posted secondary outcomes use the same general participant-count structure. Their estimates and intervals should be interpreted as separate comparisons, while recognizing that examining multiple outcomes creates more opportunities for apparently notable results. The registry does not report a multiplicity strategy or analyses for the secondary outcomes. The posted findings are therefore descriptive of the recorded comparisons, and their precision and evidential weight should not be overstated.

11. Confidence Intervals and Precision

The primary risk difference is -0.192, with a 95% confidence interval from -0.353 to -0.031. The interval is entirely below zero, so it is consistent with a lower observed event proportion in DDD60 than in DDI30 under the method used. The range remains broad enough to leave uncertainty about the magnitude of the contrast. The interval should be read as uncertainty in the estimated group difference, not as a range of individual outcomes.

The posted group proportions are 0.327 for DDI30 and 0.135 for DDD60. The registry also gives a risk ratio and an odds ratio for the primary comparison, each with its own interval. These are alternative ways to express the relative comparison and do not replace the risk difference. Because different measures have different scales, their numeric values should not be treated as interchangeable.

Precision is influenced by the amount of information available and by the variability of the outcome. With participant counts of 49 for DDI30 and 52 for DDD60, the estimates remain subject to uncertainty. The registry does not report the confidence-interval calculation method, so readers cannot assess its exact assumptions from the record alone.

For atrial fibrillation, the posted risk-difference interval extends from -0.006 to 0.331, including zero. This illustrates that a point estimate and its uncertainty can tell different parts of the story: the estimate gives a direction and size, while the interval indicates that the data are compatible with a range that includes no difference. Precision does not settle questions of clinical importance, endpoint validity, or whether multiple comparisons were considered.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on observed effects, not the trial's original design assumptions. The original sample-size justification and design assumptions are not reported in the registry record. For these binary outcomes, the figures are participants per arm, not total events. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning row uses the stated fraction of the observed effect as the effect to detect.

The 80% power column describes the planned number of participants per arm for a design intended to have an 80% chance of detecting the assumed effect under those calculation assumptions. The 90% power column gives the corresponding per-arm illustration for a design intended to have a 90% chance. These are prospective planning concepts. The displayed power values are not an assessment of the probability that the completed trial's result is correct, and they are not observed power.

Rows that plan for a smaller fraction of the observed effect require more participants per arm than rows based on the full observed effect. This is because smaller differences are harder to distinguish from random variation. The figures are therefore sensitive to the assumed effect size: planning around a large observed difference can yield smaller illustrative group sizes, while planning for a more modest difference requires larger groups.

The sample-size curve should be read as a visual expression of that same relationship between the assumed effect and the required per-arm enrollment. It is not a reconstruction of the original trial plan, and it does not establish that the completed study was adequately or inadequately sized for the investigators' intended question. The original target effect, power target, and other design choices are not reported in the registry record.

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 = 0.327; treatment proportion p₁ = 0.135; average p̄ = 0.231.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5957 = 1.1675.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5800 = 0.4881.
4. n = (1.1675 + 0.4881)² / (-0.1919)² = 74.4, rounded up to 75 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 <- 0.326530612244898                          # control proportion
p1 <- 0.134615384615385                          # 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(1463358)
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 = 75 (80% power), 100 (90% power)
 75% of observed effect: n per arm = 143 (80% power), 191 (90% power)
 50% of observed effect: n per arm = 342 (80% power), 457 (90% power)
power.prop.test: 74.4 
Simulated power at n = 75 per arm: 0.808 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when multiple outcomes, comparisons, or analyses are assessed. Even when each individual comparison uses a conventional significance threshold, examining several results increases the opportunity to observe a result that appears notable by chance. Researchers may address this through a prespecified hierarchy, adjustment procedures, or by clearly identifying analyses as exploratory. The registry record does not report a multiplicity plan, an adjustment method, or a hierarchy for the primary and secondary outcomes.

The primary outcome is a combined endpoint, and the registry lists two secondary outcomes. The record does not report component-specific analyses of the primary endpoint, or additional subgroup analyses. The number of analyses field is zero, and the secondary outcomes do not list reported analyses. This means the posted summary comparisons do not come with a documented account of which analyses were prespecified, how multiplicity was handled, or whether additional analyses were conducted but not recorded.

Missing data handling is also not reported in the registry record. The posted outcome groups include 49 participants in DDI30 and 52 in DDD60, but the record does not describe whether all randomized participants had outcome data, how incomplete follow-up was handled, or whether any imputation or sensitivity analysis was used. It does not state whether the comparisons followed an intention-to-treat, per-protocol, or other analysis population. The absence of these details prevents a full assessment of potential attrition or analysis-set bias.

These are reporting limitations, not evidence that a particular bias occurred. They make it harder to assess how robust the posted estimates are to missing outcomes, alternative analysis populations, or the examination of multiple results. A registry summary can show the reported group counts and comparisons while leaving these analytic decisions unspecified; readers should distinguish the observed numbers from conclusions that would require those missing details.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: symptomatic bradycardia (18.4%), atrio-ventricular block (16.3%), syncope (14.3%), musculoskeletal trauma (10.2%), heart failure exhacerbation (9.6%).

The registry reports serious adverse events affecting 33 of 49 participants in DDI30 and 23 of 52 in DDD60. Other adverse events affected 22 of 49 participants in DDI30 and 20 of 52 in DDD60. Deaths are listed as 2 in each group. These are group-level counts as recorded in the registry; they should not be treated as a causal comparison without additional information about event definitions, exposure, follow-up, and analysis.

The listed serious-event terms include symptomatic bradycardia at 18.4%, atrioventricular block at 16.3%, syncope at 14.3%, musculoskeletal trauma at 10.2%, heart failure exacerbation at 9.6%, and loss of pacemaker capture at 6.1%. The registry does not provide enough detail in this summary to determine how terms were selected, whether participants could contribute to more than one term, or how the term percentages relate to the group-level serious-event counts. The entries describe reported adverse-event information, not a standalone estimate of treatment-related risk.

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

The registry results show fewer participants with the primary combined endpoint in DDD60 than in DDI30 over the 2-year timeframe. The unadjusted risk difference is negative, and its confidence interval does not include zero. This describes the posted comparison for this trial and this endpoint. It does not identify which component of the combined endpoint accounts for the result, because separate primary component counts are not reported.

The randomized design supports a comparative interpretation, but the trial was not masked and the registry does not report details of endpoint adjudication, missing data, or analysis populations. These features limit how confidently the result can be generalized beyond the recorded group comparison. The registry summary also does not provide participant characteristics or a detailed account of follow-up, so it cannot establish how closely the enrolled participants match other patient groups.

The outcome should not be interpreted as a count of every episode, a measure of time until an event, or a direct estimate of the effect on each component separately. The secondary outcomes add context but include a different outcome pattern and are unadjusted. With no reported multiplicity strategy or secondary analysis details, those comparisons warrant cautious interpretation.

Statistical evidence is not the same as clinical importance. The confidence interval gives a sense of uncertainty in the group difference, while the registry does not provide a threshold for what size of difference would be important to patients or clinicians. These results alone also do not establish how the findings apply to other settings, devices, pacing strategies, or follow-up periods. The appropriate conclusion is limited to the counts, comparisons, and uncertainty reported in the registry record.

17. Why This Trial Matters Statistically

This trial illustrates how the definition of an outcome shapes the question answered by a statistical comparison. Its primary endpoint combines syncope, a specified form of presyncope, and symptomatic atrioventricular block. A single participant-level result can capture a broad symptom-related outcome, but it can conceal which component contributes most. Clear endpoint definitions are therefore essential when interpreting a group difference.

The posted estimates also show why effect measures and uncertainty belong together. A risk difference communicates an absolute contrast in event proportions, while a confidence interval shows how imprecisely that contrast is estimated. A p-value addresses a different question and should not be used as a substitute for the estimate or interval. In clinical research, judging a result involves the outcome definition, magnitude, precision, design, and context together.

The record also demonstrates the importance of transparent reporting. Randomization and a parallel-group structure are identified, but key details about masking, missing outcomes, analysis populations, multiplicity, and the original sample-size plan are not reported. Without those details, readers can describe the posted results but cannot fully evaluate all aspects of the analysis. Distinguishing what is recorded from what remains unspecified is a core part of statistical interpretation.

Finally, the planning illustrations make clear that sample-size requirements depend on the effect a future study aims to detect. Smaller target effects require more participants per arm under the stated assumptions. Those illustrations should not be confused with the design rationale or performance of the completed trial. Together, the endpoint and reporting features provide a useful example of why statistical findings need careful, bounded interpretation.

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 affect interpretation. The design is described as unmasked, so knowledge of assigned pacing strategy could influence symptom reporting or assessment. The registry does not report how endpoint events were adjudicated, whether assessment was standardized, or whether adjudicators were independent of treatment assignment. This is especially relevant because the primary endpoint includes symptom-based components.

The primary outcome combines events that differ in definition and clinical nature. The registry does not report counts for each component, so the contribution of syncope, presyncope, or symptomatic atrioventricular block cannot be separated. The secondary symptomatic episode outcome overlaps with the primary endpoint but uses a different definition. The registry also does not report the timing of events or the number of recurrent episodes.

Participant characteristics, baseline comparability, adherence, participant flow, missing-outcome handling, and the analysis population are not reported in the registry record. The original sample-size justification, planned statistical methods, and multiplicity approach are also not reported. These omissions limit assessment of generalizability, potential bias after randomization, and the robustness of the posted estimates.

The reported comparisons are unadjusted. The registry lists secondary outcomes but no reported analyses for them, and does not explain how multiple outcomes were handled. The available information supports a description of the recorded group counts and contrasts, but not a complete reconstruction of the trial analysis or protocol. These limitations should be understood as gaps in the registry record, rather than as proof that the corresponding procedures were absent.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Prevention of Syncope by Cardiac Pacing in Patients With Bifascicular Block — NCT01463358.
• Registry record last updated 2021-04-19; status last verified 2021-03.
• Results first posted 2021-04-19.
• 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 describes a completed, randomized, parallel-group trial with no masking, evaluating bradycardia pacing in patients with bifascicular block and syncope of unexplained origin. DDI30 is described as backup pacing only with a lower rate of 30 ppm; DDD60 is full pacing support with a lower rate of 60. The primary combined endpoint counts participants with syncope, specified presyncope, or symptomatic atrioventricular block over 2 years.

The primary outcome count is 16 of 49 for DDI30 and 7 of 52 for DDD60. The posted unadjusted risk difference for DDD60 compared with DDI30 is -0.192, with a 95% confidence interval from -0.353 to -0.031. The registry also lists secondary outcomes for first symptomatic syncope or presyncope and atrial fibrillation. Important details about missing data, analysis populations, multiplicity, and the original sample-size rationale are not reported in the registry record.