PROTECT-PACE STUDY - The Protection of Left Ventricular Function During Right Ventricular Pacing: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for PROTECT-PACE STUDY - The Protection of Left Ventricular Function During Right Ventricular Pacing (NCT00461734), a randomized na study. The primary outcome is Change in Left Ventricular Ejection Fraction From Baseline to 2 Years (Intent to Treat Cohort)..

2. Clinical Question

The study asks whether the location of a right ventricular pacing lead is associated with a different change in left ventricular ejection fraction over follow-up. The comparison is between the traditional right ventricular apex location and the right ventricular high septum location. The registry describes the intended population as patients who require pacemaker implantation for complete heart block.

This is a comparison of pacing locations, not a comparison of pacemaker implantation with no pacing. The primary endpoint measures change in a cardiac function measure over time. The registry also lists outcomes concerning atrial tachyarrhythmia, heart failure, mortality, stroke and brain natriuretic peptide, but those outcomes do not replace the primary question.

3. Trial Design

The registry describes PROTECT-PACE as a randomized, single-masked, parallel-group study. It is marked completed, with enrollment of 248. The study start is recorded as 2007-08 and primary completion as 2013-10. The registry lists the phase as NA. Which individuals were masked is not reported in the registry record.

The two groups differed by right ventricular lead location: RV Apex and RV High Septum. The registry summary explains that the apex was the traditional and most frequently used location, while the high septum was less commonly used. The study was intended to compare whether lead position was associated with better maintenance of heart function. The registry does not provide further details about how randomization was generated, whether allocation was concealed, or how implantation and follow-up were standardized.

The primary endpoint was change in left ventricular ejection fraction from baseline to 2 years, assessed in the intent-to-treat cohort with data available. The posted primary results contain 88 observations in each group. This endpoint-specific information should not be treated as a description of every randomized participant or as a complete accounting of follow-up. Reasons for missing endpoint data and the handling of missing values are not reported in the registry record.

The registry lists a 5-year follow-up study extension for all-cause mortality. Other secondary outcomes include device-recorded atrial tachyarrhythmia at 2-year follow-up and outcomes related to heart failure, stroke and brain natriuretic peptide. The registry lists 14 outcome measures and 10 analyses, while the posted secondary results cover 12 outcomes. Details of the protocol, the original statistical analysis plan and the trial's own sample-size justification are not reported in the registry record.

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: Partecipants initially assessed for eligibility were 248 of whom 8 were excluded before the randomization due to the following causes: * 4 failed inclusion/exclusion criteria * 2 cheanged medical condition resulting no longer eligible * 1 had a non-pacemaker procedure * 1 the site was aware of his/her randomization code in the envelope

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intent to Treat Cohort with data available

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 From Baseline to 2 Years (Intent to Treat Cohort)., measured over At 2-year follow-up.

The primary endpoint is change in left ventricular ejection fraction from baseline to 2 years, measured in the intent-to-treat cohort with data available. Left ventricular ejection fraction is a measure of how much blood the left ventricle ejects with each contraction. The registry reports the endpoint as a mean change, with standard deviations, in units of percentage.

Change from baseline uses each participant's starting measurement as a reference and focuses on how the measure changes during follow-up. Comparing the mean change between randomized groups addresses whether the observed trajectory differed according to lead-placement assignment. This is relevant to the study's stated aim of evaluating the protection of left ventricular function during right ventricular pacing.

A group mean describes the average change, not the experience of every participant. The standard deviation describes how dispersed individual measurements are around the group mean. Those summaries do not show the full distribution of values, and the posted record does not report endpoint results for participants without available data. The registry's title and stated follow-up specify the clinical measure and time point, but the rationale for choosing this endpoint over other possible measures is not reported in the registry record.

7. Results Posted in the Registry

• RV High Septum: mean -3.43 versus -2.29 on control; difference -1.14 (95% CI -3.95 to 1.67), standardized effect d = -0.12; z-test p = 0.426.

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.

Incidence of Atrial Tachyarrhythmia Recorded by the Pacemakers (Intent to Treat Cohort)

• 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:
  • RV High Septum: mean 24.11 versus 56.47 on control; difference -32.36 (95% CI -37.91 to -26.81), standardized effect d = -1.70; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for RV High Septum than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Incidence of Atrial Tachyarrhythmia Recorded by the Pacemakers (Per Protocol Cohort)

• 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:
  • RV High Septum: mean 6.66 versus 40.98 on control; difference -34.32 (95% CI -38.43 to -30.21), standardized effect d = -2.14; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for RV High Septum than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

All Cause Mortality

• 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:
  • RV High Septum: 13.6% (11/81) versus 17.9% (14/78) on control; risk difference -4.4 percentage points (95% CI -15.7 to 7.0), risk ratio 0.76 (0.37–1.56); unadjusted two-proportion z-test p = 0.449.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between RV High Septum and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results cover different types of outcomes and follow-up periods, so they do not form a single common measure of benefit or harm. The posted record includes device-recorded atrial tachyarrhythmia at 2-year follow-up, all-cause mortality at 5-year follow-up, and outcomes related to heart failure, stroke and brain natriuretic peptide. The amount and type of result information available vary across these outcomes.

Across the posted secondary analyses, the recalculated summaries and registry-reported tests do not always produce the same statistical impression. In particular, the summary-based comparisons for the device-recorded outcome differ from the registry's reported rank-based tests. This is a reminder that the choice of estimand and statistical method matters: a comparison of means is not identical to a rank-based comparison. The mortality estimate also has uncertainty, and the registry does not list a sponsor-reported test for that outcome.

These secondary findings do not overturn or confirm the primary result. They address additional questions and may be useful for describing patterns, but they are not a substitute for the prespecified primary comparison. The registry record does not report an adjustment for multiple testing. When many outcomes or analyses are examined, some results may appear noteworthy by chance, so isolated secondary p-values carry less weight than a result supported by a prespecified analysis and consistent evidence.

The registry lists more outcome measures than the number of secondary results posted in the record. For outcomes without posted estimates, the result is not reported in the registry record. It is therefore not possible to treat missing results as evidence of no effect or to infer how the unreported outcomes relate to the primary endpoint.

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

• Incidence of Atrial Tachyarrhythmia Recorded by the Pacemakers (Intent to Treat Cohort)
• Incidence of Atrial Tachyarrhythmia Recorded by the Pacemakers (Per Protocol Cohort)
• Incidence of Atrial Tachyarrhythmia Recorded by the Pacemakers (Intent to Treat Cohort)
• Incidence of Atrial Tachyarrhythmia Recorded by the Pacemakers (Per Protocol Cohort)
• Worsening of Heart Failure
• All Cause Mortality
• Incidence of Stroke
• Brain Natriuretic Peptide Levels (Intent to Treat Cohort)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary comparison is between two independent randomized groups. The outcome is continuous: each participant has a measured change in left ventricular ejection fraction, and the registry reports a group mean and standard deviation. A mean difference places the two group averages on the original outcome scale, which makes the contrast interpretable in the same units as the endpoint.

What does the mean difference describe?

The recalculated contrast is defined as the RV High Septum mean minus the RV Apex mean. A negative value means the observed mean change was lower in the high-septal group on this subtraction scale. The direction depends on which group is subtracted from which; reversing the order would reverse the sign but not change the underlying group comparison. The contrast is an average comparison, not a claim that every participant's outcome moved in that direction.

What does the standard deviation add?

The standard deviation describes the spread of individual changes around a group mean. It is not the uncertainty in the mean itself and is not a confidence interval. When individual outcomes vary widely, a difference between group averages can be estimated less precisely unless the amount of information is sufficient to overcome that variability. The posted primary summaries report a standard deviation for each group.

How is the recalculated comparison obtained?

The recalculated analysis uses the posted group means, standard deviations and available sample sizes to form a simple, unadjusted comparison of means. It does not incorporate participant-level records, covariate adjustment, stratification, repeated-measures structure or any other adjustment unless that information is already represented in the posted summaries. Such details are not reported in the registry record. The recalculated p-value and confidence interval should therefore be understood as a check based on the available summaries, not as a reconstruction of every feature of the trial's analysis.

The registry reports a two-sided z-test for the primary comparison. A two-sided test assesses evidence for a difference in either direction. The registry does not report the test's estimate, confidence interval or additional analysis details. The registry's reported analysis and the unadjusted recalculation are distinct: the former is the trial analysis as posted, while the latter is calculated from the group summaries.

What does a p-value say?

In general, a p-value describes how incompatible the observed data are with a specified no-difference model, under the assumptions of the test. It is not the probability that the no-difference model is true, and it does not measure the size or clinical importance of an effect. A larger p-value does not prove equivalence. Interpretation should consider the estimated difference and its confidence interval, not the p-value alone.

Why does the confidence interval matter?

In general, a confidence interval expresses statistical uncertainty around an estimate under the method's assumptions. A narrower interval indicates greater precision; a wider interval permits a broader range of underlying effects. For the primary contrast, the interval covers both negative and positive values. That means the summaries do not sharply distinguish between possible directions of the group difference. The interval does not account for uncertainties that are not represented in the calculation, such as bias from missing outcome data.

Why can secondary analyses differ?

Some secondary outcomes are continuous and are summarized with means and standard deviations, while mortality is reported as a count and analyzed with a risk-difference recalculation. The registry's reported secondary tests for device-recorded atrial tachyarrhythmia use the Wilcoxon (Mann-Whitney) method. In general, this rank-based method compares the ordering of observations rather than directly testing a difference between means. It can therefore answer a different statistical question from a mean-based recalculation. It is also sensitive to features of the outcome distribution and does not automatically estimate a mean difference.

For continuous outcomes, over-dispersion means that variability is greater than a model assumes. In general, failing to account for extra variability can make uncertainty appear too small; suitable models or robust methods can address this, depending on the data and design. The registry record does not report whether over-dispersion was assessed or whether models beyond the listed analyses were used.

Binary outcomes, such as whether a participant died during the stated follow-up, are summarized with counts and can be compared using risk differences or other measures. The recalculated risk difference is an absolute contrast between observed proportions. It is not interchangeable with a mean difference, and its precision depends on the event counts and group sizes. No separate sponsor-reported analysis is listed for the posted mortality outcome.

The registry does not report enough detail to establish the prespecified analysis hierarchy, adjustments for multiple testing, treatment of missing data, or whether analyses were adjusted for baseline values. These omissions limit how fully the posted results can be assessed, particularly for secondary outcomes. The simple recalculations should be treated as descriptive statistical checks rather than substitutes for an unavailable full analysis plan.

11. Confidence Intervals and Precision

The 95% confidence interval for the recalculated primary mean difference is -3.949 to 1.669. The point estimate is -1.14, but the interval extends across zero and includes values in both directions. It therefore indicates limited precision about the direction and size of the difference. The result is compatible with a range of possible group contrasts under the recalculation's assumptions.

In general, a confidence interval is a range produced by a statistical procedure designed to cover the underlying parameter at a stated long-run rate if the assumptions hold. It is not a guarantee that the true effect lies in the interval, nor does it assign a probability to individual values after observing the data. The interval also does not express whether a difference is important to patients; that requires a clinical interpretation and a relevant threshold, which are not reported in the registry record.

The observed standard deviations indicate that individual changes vary within both groups. Variation among participants contributes to uncertainty in the estimated difference. The available endpoint counts are 88 in each group, but the registry record does not explain why the primary endpoint is available for those participants or what happened to participants without endpoint data. The confidence interval therefore describes uncertainty for the reported analysis, not all potential uncertainty from missingness or study conduct.

The registry's reported primary p-value and the recalculated p-value are close, but p-values do not replace the interval. The interval makes clear that the estimate is not precise enough to establish a narrow range of plausible differences. The record does not report a clinically meaningful margin against which to judge whether the interval rules out important effects.

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 illustrations express required sample size as participants per arm for 80% power or participants per arm for 90% power. They are not total sample sizes. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each illustration uses the stated fraction of the observed effect as the effect to detect. These assumptions describe the illustrations, not the trial's original design; the trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a planning scenario in which the specified effect would be detected with 80% power, under the stated assumptions. The 90% power column uses a higher target probability of detecting that effect, again under those assumptions. Neither column describes the probability that the completed trial's result is correct. The planning figures are illustrative and depend on the assumed effect, variability and analysis model.

Rows planning for 75% or 50% of the observed effect consider progressively smaller effects than the row based on 100% of the observed effect. Smaller effects generally require more participants to detect with the same power and significance level. These figures are planning illustrations derived from the observed effect, not observed power for this completed trial. They should not be read as a retrospective measure of how likely the trial was to find its result.

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 = -1.140; pooled standard deviation σ = 9.508.
2. n = 2 × (1.96 + 0.842)² × 9.508² / -1.140² = 1,092.0, rounded up to 1,092 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 <- -1.14                      # observed difference in means
sigma <- 9.50815439504429                     # 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(461734)
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 = 1,092 (80% power), 1,462 (90% power)
 75% of observed effect: n per arm = 1,942 (80% power), 2,599 (90% power)
 50% of observed effect: n per arm = 4,368 (80% power), 5,848 (90% power)
power.t.test: 1093 
Simulated power at n = 1,092 per arm: 0.803 (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. Analyses Reported by the Sponsor

The registry reports a two-sided z-test for the primary comparison, with p = 0.435. A simple unadjusted recalculation from the posted group means, standard deviations and sample sizes gives a mean difference of -1.14, with a 95% confidence interval from -3.949 to 1.669 and an unadjusted p-value of 0.426. The registry record does not report the sponsor's primary effect estimate or confidence interval, so the posted test cannot be compared with a reported sponsor estimate on those measures.

The reported test and recalculation both indicate that the primary summaries do not provide precise evidence of a difference. The recalculation is not a replacement for the trial analysis: it uses summary statistics and may not reproduce details that depend on the participant-level data or analysis plan. The record does not explain the exact analytic choices behind the sponsor-reported test beyond identifying it as a two-sided z-test.

The discrepancy flag is false. No explanation for small numerical differences between the reported p-value and recalculated p-value is reported in the registry record. The appropriate reading is to keep the registry's analysis distinct from the simple recalculation and to interpret both alongside the estimated difference and its uncertainty.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome is identified as change in left ventricular ejection fraction from baseline to 2 years in the intent-to-treat cohort with data available. The registry also lists numerous secondary outcomes, repeated cohort descriptions for atrial tachyarrhythmia, and multiple analyses. When several hypotheses are tested, the chance of at least one apparently unusual result can increase. Statistical approaches such as a prespecified hierarchy or adjustment can address multiplicity, but the registry record does not report whether such procedures were planned or used.

The registry labels the primary population as intent-to-treat with data available. The wording identifies the intended analysis cohort but also indicates that endpoint data availability matters. The number of participants with the primary measurement is reported by group; reasons for unavailable measurements, the handling of missing values, and any sensitivity analyses are not reported in the registry record. Without those details, it is not possible to assess whether missingness could have influenced the comparison.

The record also lists a per-protocol cohort for atrial tachyarrhythmia. A per-protocol analysis can differ from an intent-to-treat analysis because it focuses on participants meeting specified adherence or protocol criteria; the actual criteria used in this study are not reported in the registry record. Results from different analysis populations should not be treated as directly interchangeable, especially when the populations differ in size or composition.

Other design and analysis details are also absent, including the randomization procedure, concealment of allocation, the identity of the masked party, baseline-adjusted analysis plans, handling of protocol deviations, and the original sample-size justification. These are not proof that methods were inadequate; they are limits on what can be evaluated from the registry record. A complete protocol and statistical analysis plan would be needed to determine which analyses were prespecified and how missing data and multiplicity were addressed.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: sob (24.2%), trauma (16.7%), death (15.8%), rectal bleeding (9.2%), raynaud's disease (9.2%).

The adverse-event record reports serious adverse events in 78 of 120 participants in the RV Apex group and 81 of 120 in the RV High Septum group. Other adverse events are reported for 6 of 120 in the RV Apex group and 0 of 120 in the RV High Septum group. These are descriptive counts as posted; they do not by themselves establish that lead location caused a difference in safety.

The record lists serious-event terms with percentages, including SOB, trauma, death, rectal bleeding, raynaud's disease and product issue. The listed percentages are 24.2%, 16.7%, 15.8%, 9.2%, 9.2% and 9.2%, respectively. The registry record does not specify in this summary how these term percentages map to groups or whether participants could contribute more than one term, so they should not be interpreted as comparative group rates.

Deaths are not reported in the adverse-event breakdown. All-cause mortality is separately posted as a secondary outcome at 5-year follow-up. Serious adverse-event summaries and mortality results address different reporting categories and should not be conflated. The registry does not provide event timing, severity grading details or an adjudication method in the information summarized.

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

The primary result estimates a small negative difference in mean change on the scale used, but the confidence interval is broad and includes values in either direction. The statistical evidence does not establish that the pacing locations differ on the primary endpoint, and it also does not establish that they are equivalent. Equivalence requires a prespecified margin and analysis that are not reported in the registry record.

The estimate concerns the average change in left ventricular ejection fraction among participants with available endpoint data in the stated analysis population. It does not describe every participant, establish why an individual outcome changed, or quantify other aspects of health. The registry's secondary results address additional outcomes but are not consistent enough in method and reporting to resolve the primary uncertainty.

Statistical uncertainty and clinical importance are different questions. A confidence interval can describe which effect sizes are compatible with an analysis, but deciding whether any such effect matters requires clinical context and a meaningful threshold. The registry record does not report such a threshold. Nor does it provide enough information about missing outcomes or multiplicity to eliminate those sources of uncertainty.

The results should therefore be read as a comparison with imprecise evidence about the primary outcome, alongside secondary and safety descriptions that need cautious interpretation. They do not justify a treatment recommendation. The registry record alone cannot establish the full balance of benefits and harms, nor can it settle what would happen in populations or settings not described in the record.

18. Why This Trial Matters Statistically

This trial illustrates a common statistical challenge in clinical research: an estimate can point in one direction while remaining too imprecise to distinguish that direction from plausible alternatives. The primary mean difference is more informative when read together with its confidence interval than when reduced to a binary interpretation of a p-value.

It also shows why the analysis method and estimand matter. A mean-based comparison and a rank-based test can answer different questions about the same continuous outcome. A recalculation from posted averages is useful as a transparent check, but it cannot reproduce analyses that depend on individual-level data or unreported model details. Keeping sponsor-reported results separate from summary-based recalculations avoids presenting them as if they were the same analysis.

The trial record also illustrates the limits of secondary-outcome interpretation. Multiple outcomes can illuminate different aspects of a study, but unadjusted findings are less secure when the number and hierarchy of tests are unclear. Missing details about the analysis plan, missing data and multiplicity matter not only for technical completeness but for how confidently results can be interpreted.

Finally, planning calculations based on an observed effect should not be confused with evidence about the completed trial's power. Such illustrations depend on assumptions and can be sensitive to the size of the effect chosen. This distinction is important when translating trial summaries into plans for future studies.

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 registry record does not report the detailed eligibility criteria, randomization procedure, allocation concealment, identity of the masked party, or implementation details for lead placement. These omissions limit assessment of how participants were selected and how the randomized comparison was conducted.

The primary endpoint is reported for an intent-to-treat cohort with data available, but reasons for unavailable measurements and the missing-data strategy are not reported. The posted summaries therefore cannot show whether missing outcome data could have altered the estimated group contrast. The record also does not report baseline endpoint values or whether the primary comparison was adjusted for baseline measurements.

For secondary outcomes, the registry includes results from both intent-to-treat and per-protocol cohorts for atrial tachyarrhythmia. The per-protocol criteria are not reported. Some sponsor-reported tests and simple summary-based recalculations differ in statistical method, and the reason for differences is not stated. The multiplicity strategy, original analysis plan and sample-size justification are also not reported.

Safety reporting is limited in the posted summary. Serious and other adverse-event counts are available, but event timing, participant-level overlap among event terms, group attribution for the listed term percentages, and detailed assessment procedures are not reported. The registry record also lists more outcomes than have posted results. These are limits of the information available in the record and should not be mistaken for evidence that the unreported analyses or procedures were absent.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: PROTECT-PACE STUDY - The Protection of Left Ventricular Function During Right Ventricular Pacing — NCT00461734.
• Registry record last updated 2017-04-25; status last verified 2017-03.
• Results first posted 2017-04-25.
• 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

PROTECT-PACE is a completed randomized, single-masked, parallel-group study comparing RV Apex with RV High Septum lead placement in patients requiring pacemakers for complete heart block. The registry reports enrollment of 248 and a primary endpoint of change in left ventricular ejection fraction from baseline to 2 years in the intent-to-treat cohort with data available.

The primary summary-based comparison is imprecise: its confidence interval includes differences in both directions. The registry also reports a two-sided z-test. Secondary outcomes and safety summaries provide additional but incomplete context; methods for multiplicity and missing data are not reported in the registry record. Conclusions should remain focused on the posted outcomes and their uncertainty.