Effects of Ivabradine on Cardiovascular Events in Patients With Moderate to Severe Chronic Heart Failure and Left Ventricular Systolic Dysfunction. A Three-year International Multicentre Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effects of Ivabradine on Cardiovascular Events in Patients With Moderate to Severe Chronic Heart Failure and Left Ventricular Systolic Dysfunction. A Three-year International Multicentre Study (NCT02441218), a randomized phase 3 study. The primary outcome is Primary Composite Endpoint: First Event Among Cardiovascular Death (Including Death of Unknown Cause) or Hospitalization for Worsening Heart Failure..

2. Clinical Question

The study objective was to demonstrate superiority of ivabradine over placebo for reducing cardiovascular mortality or hospitalization for worsening heart failure among people with chronic heart failure receiving recommended therapy. The registry reports event counts for the composite and a sponsor Cox regression analysis. Those answer related but not identical statistical questions: event counts compare whether participants had an event, while a time-to-event analysis also uses information about when events occurred.

The results describe the groups enrolled in this randomized trial and the analyses recorded for them. They do not, by themselves, establish how the findings apply to people who differ from the registry’s stated population. Specific eligibility criteria, background-treatment requirements, and subgroup questions are not reported in the registry record.

3. Trial Design

The registry identifies this as a Phase 3, randomized, quadruple-masked, parallel-group study comparing ivabradine with placebo. Its title describes it as a three-year international multicentre study. The recorded enrollment is 6505. The study start is listed as 2006-09, primary completion as 2010-04, and status as completed. The registry lists Institut de Recherches Internationales Servier as the sponsor.

The posted primary endpoint is the number of participants experiencing the first event in a composite of cardiovascular death, including death of unknown cause, or hospitalization for worsening heart failure. The recorded timeframe is all over the study, up to 42 months. The registry also posts secondary outcomes covering cardiovascular death, hospitalization for worsening heart failure, all-cause mortality, death from heart failure, hospitalization for any cause, hospitalization for a cardiovascular reason, and unplanned hospitalizations for any cause or cardiovascular reason. Results for only some of those outcomes are detailed in the registry record reviewed for this analysis; the other secondary results are not reported in the registry record.

Randomization supports a comparison between treatment groups by assigning participants rather than allowing treatment choice to determine group membership. Masking is intended to limit the influence of treatment knowledge on conduct or assessment, although which parties were masked is not reported in the registry record. The method used to generate the allocation sequence, allocation concealment procedures, detailed masking procedures, and analysis populations are also not reported in the registry record. The original sample-size justification and the trial’s prespecified statistical analysis plan 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: Following a run-in period of two weeks during which no study treatment was dispensed, the participants were randomised to receive ivabradine or placebo in addition to their usual cardiovascular treatment in double-blind treatment period.

Overall Study

Reasons for not completing this period:

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 Primary Composite Endpoint: First Event Among Cardiovascular Death (Including Death of Unknown Cause) or Hospitalization for Worsening Heart Failure., measured over All over the study (up to 42 months)..

The primary endpoint combines cardiovascular death, including death of unknown cause, with hospitalization for worsening heart failure. It counts a participant when the first of these events occurs. A composite endpoint can capture more than one clinically important type of event in a single outcome, and may yield more events for analysis than either component alone. That can make a trial’s main comparison more statistically informative, but it also means the combined result reflects the components together rather than one component in isolation.

For the primary endpoint, the registry reports 793.0 participants with an event among 3241.0 in the ivabradine group and 937.0 among 3264.0 in the placebo group. The record’s binary summary treats the endpoint as whether a participant experienced an event during the study timeframe, up to 42 months. The sponsor additionally reports a Cox regression analysis, which compares event timing as well as occurrence under its time-to-event framework.

The registry does not report the component-specific primary analysis, so the composite result cannot establish which component contributed more to the observed group difference. It also does not report how deaths of unknown cause were classified beyond their inclusion in the composite definition. These details matter when interpreting what a composite can and cannot say about its separate parts.

7. Results Posted in the Registry

• Ivabradine: 24.5% (793/3241) versus 28.7% (937/3264) on control; risk difference -4.2 percentage points (95% CI -6.4 to -2.1), risk ratio 0.85 (0.79–0.92); unadjusted two-proportion z-test p = <0.001.

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.

Cardiovascular Death

• 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:
  • Ivabradine: 13.9% (449/3241) versus 15.0% (491/3264) on control; risk difference -1.2 percentage points (95% CI -2.9 to 0.5), risk ratio 0.92 (0.82–1.04); unadjusted two-proportion z-test p = 0.173.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ivabradine and the control. The interval gives the range of effects that remain compatible with the data.

Hospitalisation for Worsening Heart Failure

• 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:
  • Ivabradine: 15.9% (514/3241) versus 20.6% (672/3264) on control; risk difference -4.7 percentage points (95% CI -6.6 to -2.9), risk ratio 0.77 (0.69–0.85); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Ivabradine 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:
  • Ivabradine: 15.5% (503/3241) versus 16.9% (552/3264) on control; risk difference -1.4 percentage points (95% CI -3.2 to 0.4), risk ratio 0.92 (0.82–1.03); unadjusted two-proportion z-test p = 0.128.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Ivabradine and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes give a mixed picture rather than a uniform pattern across all measures. The posted comparisons for hospitalization for worsening heart failure are directionally consistent with the primary composite, while cardiovascular death and all-cause mortality have estimates whose uncertainty includes no difference. This pattern is compatible with a composite result being influenced more by one component than another, but the registry does not report a formal decomposition or a component contribution analysis. The component-specific estimates should be considered on their own terms rather than inferred from the composite.

The registry lists other secondary outcomes, including death from heart failure and hospitalizations for any cause or cardiovascular reason, as well as unplanned hospitalizations. Their results are not reported in the registry record. Consequently, the overall secondary-outcome pattern cannot be characterized across every outcome named in the record.

Secondary analyses generally carry less evidential weight than the prespecified primary comparison when many outcomes are examined. Each additional comparison creates more opportunities for a seemingly notable result to arise by chance. The registry record does not report a multiplicity adjustment, a hierarchy for testing secondary outcomes, or a complete prespecified analysis plan. Thus, the posted secondary p-values should be interpreted as unadjusted unless the record states otherwise, and should not be treated as independent confirmation of the primary finding.

Different endpoints also have different meanings and event frequencies. A result for hospitalization is not interchangeable with a result for death, and a composite can conceal variation between its components. Taken together, the reported secondary outcomes help describe the range of findings but do not settle the unanswered questions about other outcomes, multiplicity, or the balance of component contributions.

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

• Cardiovascular Death
• Hospitalisation for Worsening Heart Failure
• All-cause Mortality
• Death From Heart Failure
• Hospitalisation for Any Cause
• Hospitalisation for Cardiovascular Reason
• Unplanned Hospitalisation for Any Cause
• Unplanned Hospitalisation for CV Reason

9. Statistical Interpretation

10. Statistical Methods Explained

The posted outcomes are binary participant counts: a participant either experienced the specified event during the stated timeframe or did not. For the primary composite, the registry records the number of participants with an event and the number in each group. A comparison based on these counts summarizes event occurrence, but does not incorporate when within follow-up an event happened. The primary timeframe is all over the study, up to 42 months.

What does the risk difference represent?

General statistical explanation: a risk difference subtracts the event proportion in the comparator group from the event proportion in the intervention group. It is expressed on an absolute scale, so it describes the difference in observed proportions rather than a relative change. In the posted primary comparison, the estimate is -0.042 for ivabradine relative to placebo. A negative estimate means the observed proportion was lower in the ivabradine group. The 95% confidence interval runs from -0.064 to -0.021, wholly on the negative side of zero.

A risk difference is useful because it retains an absolute scale, but it depends on the outcome and follow-up definition. It does not, on its own, describe whether events occurred earlier or later. The registry’s unadjusted comparison is recalculated from the posted summary counts; it is not a substitute for the sponsor’s time-to-event analysis.

How do relative measures differ?

General statistical explanation: a risk ratio compares the event proportions by division, while an odds ratio compares event odds. Both are relative measures and answer different questions from a risk difference. The primary recalculated risk ratio is 0.852, with a 95% confidence interval from 0.786 to 0.924. The recalculated odds ratio is 0.804, with a 95% confidence interval from 0.721 to 0.898. These estimates are unadjusted calculations from the posted counts. A relative measure below one indicates lower observed event occurrence in the intervention group on that measure, but it should not be interpreted as an absolute difference.

What does the Cox analysis add?

General statistical explanation: a Cox regression analysis is a time-to-event method. It uses event times and can account for participants whose event status is not observed through the same follow-up duration, subject to the analysis rules and assumptions. The hazard ratio is a relative comparison of event rates over time, not a risk ratio at a fixed time and not a risk difference. The sponsor reports a primary hazard ratio of 0.82, with a 95% confidence interval from 0.75 to 0.90. Details of censoring rules, model covariates, proportional-hazards assessment, and missing-time handling are not reported in the registry record.

The registry labels the reported method as Cox regression and gives the parameter as a hazard ratio. The exact specification of the model is not reported in the registry record. It is therefore not possible to determine from the registry entry whether the estimate was adjusted for particular baseline characteristics, how competing events were handled, or what diagnostics were undertaken.

How should p-values and confidence intervals be read?

General statistical explanation: a p-value describes how incompatible the observed data are with a stated null model, assuming that model and the analysis conditions are appropriate. It is not the probability that the null hypothesis is true, nor a measure of the clinical importance of an effect. The primary unadjusted p-value is < 0.001, while the sponsor reports p < 0.001 for its Cox analysis. Because the analyses use different measures and methods, their p-values should not be treated as if they came from identical calculations.

A confidence interval conveys uncertainty around an estimate under the method used to calculate it. For a risk difference, zero is the no-difference value. For a hazard ratio, one is the no-relative-difference value. An interval that includes the relevant no-difference value is compatible with a range of effects that includes no difference; it does not prove there is no effect. An interval excluding that value is evidence against the corresponding null under the model, but it does not address all sources of bias or uncertainty.

The registry also posts planning illustrations based on observed effects. They are prospective calculations under stated assumptions, not observed outcomes or evidence about the trial’s original design. The sponsor’s own analysis remains the reported trial analysis, while the unadjusted recalculations offer a separate description based on posted group counts. The registry record does not report whether the sponsor analysis was prespecified in exactly the form presented.

11. Confidence Intervals and Precision

The primary unadjusted risk-difference estimate is -0.042, with a 95% confidence interval from -0.064 to -0.021. The whole interval lies below zero, the no-difference value for a risk difference. This indicates that the estimate is not merely a single point: the posted data are compatible with a range of negative differences under the calculation method. The interval still leaves uncertainty about the size of the difference, and does not account for uncertainties that the registry does not describe, such as the analysis plan or missing-data handling.

The sponsor’s Cox analysis reports a hazard ratio of 0.82, with a 95% confidence interval from 0.75 to 0.90. The interval is below one, the no-relative-difference value for a hazard ratio. This is consistent in direction with the unadjusted risk-difference calculation, while representing a time-to-event comparison rather than an absolute difference in event proportions. The confidence interval does not make the two estimates directly interchangeable.

Precision differs across outcomes. For the unadjusted comparisons of cardiovascular death and all-cause mortality, the reported confidence intervals for risk differences include zero. Their ranges therefore include no difference as well as values on either side of it. The corresponding sponsor hazard-ratio intervals also include one. By contrast, the hospitalization-for-worsening-heart-failure estimates have intervals excluding the relevant no-difference values. This describes the statistical uncertainty in the posted analyses; it is not a ranking of clinical importance.

Confidence intervals do not capture every limitation. Their interpretation depends on the analysis method and assumptions, and the registry does not report all details needed to assess those assumptions. Nor does an interval state the probability that the true effect lies within its limits. It is best read alongside the effect scale, endpoint definition, and method used to produce it.

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 translate an assumed effect size into a sample-size requirement under a stated design calculation. For the binary outcomes, the figures are participants per arm. The listed 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 the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the assumed effect under those assumptions, if that effect and the calculation model were correct. The 90% power column uses a higher target chance of detection, so it generally requires more participants per arm for the same assumed effect. For example, the primary endpoint illustration lists 1,704 participants per arm for 80% power and 2,281 participants per arm for 90% power when planning for 100% of the observed effect.

The rows planning for 75% or 50% of the observed effect assume smaller effects than the row using 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so the calculations require more participants per arm. The figures are planning illustrations based on the observed effect, not observed power for the completed trial. They do not establish the probability that this trial detected a true effect, and should not be read as the trial’s original design requirements.

The stated method differs for time-to-event outcomes: those planning calculations give the total number of events rather than participants per arm. The sample-size assumptions should therefore be read together with the type of outcome and the unit used for its illustration. The registry record does not report further adjustments for attrition, adherence, or other design features in the original planning.

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 = 0.287; treatment proportion p₁ = 0.245; average p̄ = 0.266.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6248 = 1.2246.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6241 = 0.5252.
4. n = (1.2246 + 0.5252)² / (-0.0424)² = 1,703.7, rounded up to 1,704 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 <- 0.287071078431373                          # control proportion
p1 <- 0.244677568651651                          # 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(2441218)
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 = 1,704 (80% power), 2,281 (90% power)
 75% of observed effect: n per arm = 3,068 (80% power), 4,107 (90% power)
 50% of observed effect: n per arm = 6,988 (80% power), 9,355 (90% power)
power.prop.test: 1703.7 
Simulated power at n = 1,704 per arm: 0.798 (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

For the primary endpoint, the sponsor reports a Cox regression hazard ratio of 0.82, with a 95% confidence interval from 0.75 to 0.90 and p < 0.001. The recalculated unadjusted comparison from the posted counts gives a risk difference of -0.042, with a 95% confidence interval from -0.064 to -0.021 and p < 0.001. Both estimates point in the same direction, but they describe different quantities: the risk difference compares event proportions, whereas the hazard ratio compares event rates over time.

The record does not flag a discrepancy between its posted results and the recalculation. Where a discrepancy is flagged, the sponsor’s own analysis takes precedence; that is not the situation recorded for this trial. The recalculated results are a simple unadjusted check based on the posted summary counts, not a reconstruction of the sponsor’s full model. The registry does not report enough detail to reproduce the Cox regression or verify its exact model specification.

For the reported secondary outcomes, the sponsor’s Cox analyses are also distinct from the unadjusted binary-count calculations. Their estimates may differ because they use time-to-event information and possibly analysis details not reported in the registry record. The sponsor results should be interpreted on the hazard-ratio scale and should not be relabeled as risk ratios or absolute differences.

15. Multiplicity, Missing Data and Analysis Populations

The registry names several secondary outcomes in addition to the primary composite. Testing multiple outcomes increases the chance that one or more results will appear statistically notable by chance, even when no corresponding underlying difference exists. This is the general multiplicity problem. A prespecified testing hierarchy or statistical adjustment can address it in some ways, but the registry record does not report a multiplicity plan or adjustment for the posted secondary analyses.

Without that information, secondary p-values should be treated as descriptive and unadjusted, rather than as a family of confirmatory tests. The record also does not report whether any outcomes were selected for emphasis after results were known, or whether all planned outcomes and analyses are represented. The number of outcome measures and analyses is recorded as 10, but that alone does not establish how the analyses were planned or interpreted.

Missing-data procedures are not reported in the registry record. In particular, the record does not explain how participants without complete follow-up were handled, how censoring was defined for the Cox analyses, or whether the event-count analyses used any imputation or other strategy for missing endpoint status. These details can affect both estimates and uncertainty.

Analysis populations are also not reported in sufficient detail. The registry gives the group counts used in the endpoint summaries, but does not state whether the analysis followed an intention-to-treat population, a per-protocol population, or another definition. Specific exclusions after randomization and their handling are not reported in the registry record. These omissions limit assessment of whether the posted comparisons preserve the randomized allocation and how robust the findings are to missingness or departures from assigned treatment.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cardiac failure (20.4%), atrial fibrillation (3.9%), angina unstable (3.7%), sudden death (3.7%), sudden cardiac death (2.3%).

The registry reports serious adverse event figures separately by group. In the ivabradine group, 1369 participants were affected among 3232 at risk; in the placebo group, 1481 were affected among 3260 at risk. The record also reports other adverse event figures: 2062 among 3232 at risk for ivabradine and 2020 among 3260 at risk for placebo. These are counts in the registry’s adverse-event summary, not estimates adjusted for follow-up time or a comparison accounting for differences in exposure.

The registry lists cardiac failure at 20.4%, atrial fibrillation at 3.9%, unstable angina at 3.7%, sudden death at 3.7%, sudden cardiac death at 2.3%, and pneumonia at 2.2% among its top serious terms. Arm-specific figures for those terms are not reported in the registry record, and the denominator used for each percentage is not stated in the posted summary. Death counts in the adverse-event fields are not reported in the registry record.

These summaries do not give event timing, severity grades beyond the serious-event category, relatedness assessments, or a complete account of how adverse events were collected. They should be read as descriptive registry figures, not as a complete comparative safety analysis.

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

The primary endpoint results show fewer observed composite events in the ivabradine group than in the placebo group, with the unadjusted risk-difference interval excluding zero and the sponsor’s Cox interval below a hazard ratio of one. The results therefore describe a group difference in the posted primary analysis, with the sponsor’s time-to-event estimate and the unadjusted count-based estimate agreeing in direction. They do not establish that every participant would experience the same outcome or that the observed difference applies to people outside the trial population.

The composite combines cardiovascular death and hospitalization for worsening heart failure. A result for the combined endpoint does not show that both components changed in the same way, or by the same amount. The registry reports secondary results for some components, but it does not provide the component-specific primary analysis or all secondary results listed among the planned outcomes.

Statistical evidence should not be confused with clinical importance. A p-value and confidence interval describe evidence and uncertainty under an analysis method; they do not determine whether the magnitude of a difference matters to patients or clinicians. The registry record does not provide a threshold for clinical importance, detailed quality-of-life results, or a full accounting of treatment burden and safety needed for a broader benefit-risk judgment.

The findings also do not answer questions about long-term outcomes beyond the recorded follow-up, different dosing approaches, or specific patient subgroups unless those analyses are reported separately. Missing details about analysis populations, missing data, multiplicity, and model specification further constrain interpretation. The posted statistics are one part of a clinical evidence assessment, not a standalone treatment recommendation.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definition and analysis scale matter. The primary outcome is a composite of death and hospitalization, and the registry supplies both event counts and a sponsor time-to-event analysis. The count-based risk difference communicates an absolute group contrast, while the hazard ratio summarizes a relative comparison over time. Their agreement in direction is informative, but they are not duplicate estimates and should not be compared as though they measured the same quantity.

The secondary outcomes also show why a composite should not be assumed to represent each component equally. The findings for hospitalization for worsening heart failure are more clearly separated from the no-difference value than the posted mortality comparisons. Without a formal component analysis, the primary composite cannot identify which part is responsible for the pattern. Multiple secondary outcomes add context but also raise multiplicity concerns when no adjustment plan is reported.

The registry’s planning illustrations demonstrate the relationship between an assumed effect and sample-size requirements. Calculations based on a smaller target effect require more participants per arm, and higher target power also generally requires more participants. These are planning calculations based on the observed effect, not the original design rationale and not a measure of the completed trial’s observed power.

Finally, the record is a reminder that numerical results need documentation of the statistical plan, analysis populations, missing-data handling, and safety definitions. Where such details are absent, careful interpretation means distinguishing what the posted data show from what remains uncertain.

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 entry does not report the full eligibility criteria, dose and administration details, background-treatment requirements, or detailed arm descriptions. The title describes an international multicentre study, but the registry information summarized for this analysis does not provide site-level enrollment or country-specific results. The trial’s original sample-size rationale and prespecified statistical analysis plan are not reported in the registry record.

For the primary endpoint, the registry provides a composite count and a sponsor time-to-event analysis, but not a primary analysis separated by component. The full Cox model specification, covariates, censoring rules, proportional-hazards assessment, and handling of competing events are not reported. The registry also does not specify the analysis populations or how missing outcome data were addressed.

Multiplicity handling is not reported, which limits the confirmatory interpretation of secondary comparisons. Results are not reported in the registry record for all secondary outcomes listed. Some secondary estimates have confidence intervals that include the no-difference value; these results do not establish equivalence or rule out potentially relevant differences. The posted record does not provide a clinical importance threshold to contextualize the estimates.

Adverse-event summaries lack detail about event definitions, timing, exposure duration, relatedness, and arm-specific breakdowns for the listed serious terms. Death counts in the adverse-event fields are not reported in the registry record. These gaps mean the posted safety figures cannot serve as a complete comparative safety assessment. The findings should therefore be interpreted within the specific endpoints and analyses documented, with the unreported elements kept distinct from evidence of no effect or no risk.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effects of Ivabradine on Cardiovascular Events in Patients With Moderate to Severe Chronic Heart Failure and Left Ventricular Systolic Dysfunction. A Three-year International Multicentre Study — NCT02441218.
• Registry record last updated 2020-01-03; status last verified 2020-01.
• Results first posted 2015-06-29.
• 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 Phase 3 randomized, quadruple-masked, parallel-group comparison of ivabradine and placebo in chronic heart failure. Enrollment is recorded as 6505, with a study start of 2006-09 and primary completion of 2010-04. The primary endpoint is the first occurrence of cardiovascular death, including death of unknown cause, or hospitalization for worsening heart failure, over the study up to 42 months.

The posted primary count-based estimate favors a lower observed event proportion in the ivabradine group, and the sponsor’s Cox analysis reports a hazard ratio below one. Secondary findings are mixed, and the registry does not report multiplicity handling, full analysis-population definitions, or missing-data procedures. The safety summary provides group-level counts but limited detail on event definitions and term-specific comparisons. These results describe the record’s analyses and should be interpreted alongside the information that is not reported.