Effect of Dalcetrapib vs Placebo on CV Risk in a Genetically Defined Population With a Recent ACS: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Dalcetrapib vs Placebo on CV Risk in a Genetically Defined Population With a Recent ACS (NCT02525939), a randomized phase 3 study. The primary outcome is Composite of Cardiovascular Death, Resuscitated Cardiac Arrest, Non-Fatal Myocardial Infarction, and Non-Fatal Stroke.

2. Clinical Question

This question concerns a composite outcome: a participant was counted at the first occurrence of any listed component. The primary endpoint therefore combines several clinically distinct events into a single measure of time to an event. The registry record identifies the population as all subjects randomized to treatment and reports a median follow-up duration of 39.9 months.

The clinical question is specific to the trial’s selected population. It does not address people without the genetic profile, people who were not recently hospitalized for acute coronary syndrome, or outcomes beyond those defined in the endpoint. The study was randomized and placebo-controlled, making the comparison between assigned groups central to interpreting the posted results. Its outcome findings describe the measured trial population and follow-up, rather than establishing what would occur in other populations or settings.

3. Trial Design

Dal-GenE was a Phase III, randomized, parallel-group, placebo-controlled study sponsored by DalCor Pharmaceuticals. The registry lists an enrollment of 6147 and records the trial as completed. The start is listed as 2016-04 and primary completion as 2021-10. Participants had recently been hospitalized for acute coronary syndrome and had to have the appropriate genetic profile; the registry summary describes testing for the AA genotype.

The study compared dalcetrapib with matching placebo. The dalcetrapib group received 600 mg orally once daily, as two 300 mg tablets. The placebo group received matching tablets once daily. The registry classifies masking as quadruple, while its brief summary describes the study as double-blind. Both descriptions indicate masking, but the registry record does not explain the roles included in its masking classification.

Screening could take place at the time of the index acute coronary syndrome event or later, and enrollment could begin in hospital and continue after discharge. Randomization had to occur within 4-12 weeks after the index event. Participants were assessed based on medical history, and those likely to qualify underwent genotype testing. The registry record does not report the detailed randomization procedure, allocation concealment process, site count, or the original protocol’s sample-size justification.

The posted primary endpoint was evaluated from randomization until the first occurrence of any component, with median follow-up of 39.9 months. The registry also reports two secondary composite outcomes. The reported primary analysis used a stratified Cox proportional hazard model. Details of the stratification factors and additional model implementation 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: A total of 6149 eligible patients underwent randomization, among whom two were randomized by error and excluded.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All subjects randomized to treatment

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 Composite of Cardiovascular Death, Resuscitated Cardiac Arrest, Non-Fatal Myocardial Infarction, and Non-Fatal Stroke, measured over From randomization to the first occurrence of any component of the composite primary endpoint (median duration of follow-up was 39.9 months).

The primary endpoint measures time from randomization to the first occurrence of cardiovascular death, resuscitated cardiac arrest, non-fatal myocardial infarction, or non-fatal stroke. The registry says each efficacy endpoint was adjudicated by an independent clinical endpoint committee, and the primary event was required to be positively adjudicated by that committee.

A composite endpoint can capture several types of clinically important events in one outcome. For a time-to-first-event analysis, the participant contributes the time up to the first qualifying component; later components do not create additional primary events for that participant. This approach makes the endpoint a measure of when any component first occurs, not a separate estimate for each component and not a measure of total events.

Composite outcomes are often used to evaluate a broader set of events than any single component would capture. Their interpretation depends on the components: they may differ in severity, frequency, and clinical meaning. The registry record does not report component-specific primary outcome counts in the registry record for interpretation, so the overall composite result cannot establish which component contributed most to the observed event count or treatment comparison.

The registry reports participants with events by arm as well as a time-to-event model. These are related but not identical summaries. Counts describe how many participants had an event during observed follow-up; a Cox model uses event timing and follow-up information to estimate a relative hazard under its modeling assumptions.

7. Results Posted in the Registry

• Dalcetrapib: 9.5% (292/3071) versus 10.6% (327/3076) on control; risk difference -1.1 percentage points (95% CI -2.6 to 0.4), risk ratio 0.89 (0.77–1.04); unadjusted two-proportion z-test p = 0.144.

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.

Composite Endpoint of Cardiovascular Death, Resuscitated Cardiac Arrest, Non-Fatal Myocardial Infarction, Non-Fatal Stroke, Hospitalization for ACS (With Electrocardiogram Abnormalities) or Unanticipated Coronary Revascularization

• 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:
  • Dalcetrapib: 15.3% (471/3071) versus 15.3% (471/3076) on control; risk difference 0.0 percentage points (95% CI -1.8 to 1.8), risk ratio 1.00 (0.89–1.13); unadjusted two-proportion z-test p = 0.978.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dalcetrapib and the control. The interval gives the range of effects that remain compatible with the data.

Composite Endpoint of Cardiovascular Death, Resuscitated Cardiac Arrest, Non-Fatal Myocardial Infarction, Non-Fatal Stroke or Hospitalization for New or 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:
  • Dalcetrapib: 10.5% (321/3071) versus 11.2% (346/3076) on control; risk difference -0.8 percentage points (95% CI -2.4 to 0.8), risk ratio 0.93 (0.81–1.07); unadjusted two-proportion z-test p = 0.316.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dalcetrapib and the control. The interval gives the range of effects that remain compatible with the data.

The two posted secondary composites do not show a uniform pattern of clear separation between the treatment groups. One combines the primary endpoint components with hospitalization for acute coronary syndrome with electrocardiogram abnormalities or unanticipated coronary revascularization. The other combines the primary components with hospitalization for new or worsening heart failure. Their reported hazard-ratio intervals include 1.00, and their p-values are 0.95 and 0.27, respectively.

These secondary outcomes broaden the event definitions beyond the primary endpoint. They can add context about related cardiovascular events, but they are not interchangeable with the primary composite. Their additional components may occur with different frequencies and may carry different clinical implications. The registry record does not provide component-specific results that would show which events drove either secondary composite.

The overall pattern is consistent with the primary result in that the posted secondary analyses do not establish a clear between-group difference. That consistency does not independently confirm the primary result: secondary endpoints are additional questions, and their interpretation depends on how they were prespecified and tested. The registry record does not report a multiplicity-adjustment procedure for the secondary outcomes.

When multiple outcomes are tested, the chance of obtaining at least one apparently unusual result can increase, depending on the testing strategy. Unadjusted secondary p-values do not account for that issue. They should therefore carry less inferential weight than the designated primary endpoint and should be treated as exploratory unless the analysis plan establishes otherwise. The registry record does not report whether these secondary analyses were confirmatory, how their order was specified, or how multiplicity was addressed.

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

• Composite Endpoint of Cardiovascular Death, Resuscitated Cardiac Arrest, Non-Fatal Myocardial Infarction, Non-Fatal Stroke, Hospitalization for ACS (With Electrocardiogram Abnormalities) or Unanticipated Coronary Revascularization
• Composite Endpoint of Cardiovascular Death, Resuscitated Cardiac Arrest, Non-Fatal Myocardial Infarction, Non-Fatal Stroke or Hospitalization for New or Worsening Heart Failure

9. Statistical Interpretation

10. Statistical Methods Explained

The registry presents the primary outcome in two statistical forms: participant counts with an event and a time-to-event comparison. Each answers a related but distinct question. Counts and unadjusted risk measures compare whether participants experienced an event during follow-up. The stratified Cox proportional hazard model compares event timing while accounting for follow-up information through a hazard-based approach.

What does the risk difference mean?

The risk difference subtracts the event proportion in the placebo group from the event proportion in the dalcetrapib group. A negative estimate means the observed proportion was lower in the dalcetrapib group; a positive estimate would mean it was higher. For the primary outcome, the estimate is -0.011. This is an unadjusted difference in event proportions based on the posted counts, not an adjusted treatment effect from the Cox model. The interval from -0.026 to 0.004 describes the uncertainty around this estimate under the calculation used.

A risk ratio compares the two event proportions as a ratio, while an odds ratio compares event odds. These measures use the same arm-level event counts but express the comparison on different scales. Their values are not interchangeable with a hazard ratio. For example, the risk ratio of 0.894 is an unadjusted comparison of event proportions; the sponsor-reported hazard ratio of 0.88 is from a model of time to event.

Why use a time-to-event model?

Participants may have different lengths of observation, and the timing of events can carry information beyond whether an event was recorded. A time-to-event method uses the observed event times and the follow-up information available for participants. In a Cox proportional hazard model, the hazard ratio summarizes the relative event rate over time, conditional on the model’s structure. It does not directly give the probability that a participant will have an event, and it is not an absolute risk difference.

The registry reports a stratified Cox proportional hazard model for the primary endpoint. Stratification allows the comparison to be made within specified strata, but the stratification factors are not reported in the registry record. The model also relies on assumptions, including proportional hazards for a single hazard ratio to be a suitable summary over follow-up. Diagnostics or checks of that assumption are not reported in the registry record. The term “stratified” does not by itself reveal which variables were used or how they were handled.

How should the p-values be read?

A p-value measures how unusual the observed data, or data more extreme, would be under a specified null model and analysis. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The registry reports p = 0.12 for its primary Cox analysis. The unadjusted re-calculation gives p = 0.144 for the difference in event proportions. These values come from different analyses and should not be treated as competing estimates of the same model result.

Statistical significance is not a boundary between certainty and uncertainty. Interpretation should consider the estimate, the confidence interval, the outcome definition, the design, and the analysis plan. The registry record does not report the full prespecified statistical analysis plan or the significance threshold used for the sponsor’s primary analysis.

Why do confidence intervals matter?

A confidence interval gives a range of estimates compatible with the observed data under the method’s assumptions and repeated-sampling framework. A wider interval indicates less precision; an interval spanning the null value indicates that the data do not rule out that value at the stated confidence level. For the hazard ratio, the 95% interval is 0.75 to 1.03 and includes 1.00. For the risk difference, the 95% interval is -0.026 to 0.004 and includes 0. The two intervals use different measures and null values.

Confidence intervals do not include every source of uncertainty. They do not, by themselves, account for bias from missing data, outcome ascertainment, deviations from the analysis plan, or model misspecification. The registry reports independent endpoint adjudication, but other implementation details needed to assess these sources are not reported in the registry record.

Why can over-dispersion matter in other outcome types?

General statistical explanation: a count model can be too optimistic if it assumes that variation is explained entirely by its chosen mean structure when the data vary more than that model allows. This extra variability is called over-dispersion. It can make standard errors too small and confidence intervals too narrow if ignored. The posted primary endpoint is a count of participants with an event, and its reported sponsor analysis is a time-to-event model; over-dispersion is not identified as a feature of these analyses. The registry record does not report a count-regression analysis for the primary endpoint.

For binary outcomes, the event indicator records whether each participant had the defined event, while the arm-level event proportion summarizes those indicators. A composite binary count does not capture event timing and does not tell how many events an individual participant experienced. That is why the posted count-based re-calculation and the Cox analysis provide complementary but distinct descriptions.

Finally, endpoint adjudication can support consistent application of event definitions by having an independent committee evaluate events. It does not remove uncertainty in estimates or replace information about missing observations, censoring, analysis populations, and model assumptions. Those details remain important for a complete assessment of the result.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data locate an effect estimate. The primary hazard ratio reported by the registry is 0.88, with a 95% confidence interval from 0.75 to 1.03. Since the interval includes 1.00, the estimate is compatible with a range that includes equal hazards as well as values on either side of that reference. The point estimate alone should not be read as a definitive difference.

The unadjusted risk difference is -0.011, with a 95% confidence interval from -0.026 to 0.004. Zero is the null value for a risk difference, and it lies within this interval. The interval therefore does not exclude no difference in the observed event proportions. The unadjusted risk ratio interval, 0.770 to 1.039, includes 1.00; the odds ratio interval, 0.748 to 1.043, also includes 1.00.

These intervals differ because they describe different effect measures and analyses. The Cox interval concerns a model-based relative hazard over time; the re-calculated intervals concern unadjusted comparisons of event proportions. The registry’s median follow-up was 39.9 months, but the available record does not give a full account of censoring or individual follow-up patterns.

Confidence intervals express sampling uncertainty under their methods. They do not show the probability that a particular effect is true, and they do not resolve issues such as missing data or model assumptions. The posted estimates are consequently best read with their interval widths, outcome definition, and analysis method in view.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design calculation. The sample-size assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial’s design assumptions and sample-size justification are not reported in the registry record.

For these participant-count outcomes, the figures are participants per arm, not total events. The sample-size assumptions distinguish time-to-event illustrations, which use total events, from other outcomes, which use participants per arm. The outcomes discussed in the posted planning figures are participant event counts. Thus, a per-arm figure describes the number of participants that a hypothetical study would plan for in each group under the stated assumptions, not a count of events observed in Dal-GenE.

The 80% power column describes the planned group size associated with an 80% chance of detecting the specified effect under the illustration’s assumptions, if that effect and model assumptions apply. The 90% power column describes the corresponding planning target for a 90% chance. These are design probabilities for a hypothetical study, not probabilities that the observed finding is correct. This is not observed power.

Each row uses a different fraction of the observed effect. Planning for a smaller effect requires more participants per arm because smaller differences are harder to distinguish from random variation. The figures are sensitive to the effect chosen and assumptions used; they should not be treated as a reconstruction of the trial’s protocol or its actual planning rationale.

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 = 0.106; treatment proportion p₁ = 0.095; average p̄ = 0.101.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4256 = 0.8341.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4255 = 0.3581.
4. n = (0.8341 + 0.3581)² / (-0.0112)² = 11,283.0, rounded up to 11,283 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 <- 0.10630689206762                          # control proportion
p1 <- 0.095083034842071                          # 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(2525939)
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 = 11,283 (80% power), 15,105 (90% power)
 75% of observed effect: n per arm = 20,308 (80% power), 27,186 (90% power)
 50% of observed effect: n per arm = 46,249 (80% power), 61,913 (90% power)
power.prop.test: 11283 
Simulated power at n = 11,283 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s reported primary analysis is the stratified Cox proportional hazard model, with hazard ratio 0.88, 95% confidence interval 0.75 to 1.03, and p = 0.12. This is the sponsor-reported time-to-event result and is the relevant primary inferential analysis in the record.

The unadjusted re-calculation uses the posted event counts to compare proportions. It gives a risk difference of -0.011, with a 95% confidence interval from -0.026 to 0.004, and p = 0.144. The recalculation is not a reproduction of the Cox analysis: it does not use event timing or the model’s stratification. Its role is to provide a simple count-based comparison, not to supersede the sponsor’s time-to-event analysis.

The registry reports no discrepancy between the sponsor analysis and the recalculation. The estimates are directionally similar, but they are expressed on different scales and arise from different methods. They should therefore be interpreted as complementary descriptions rather than identical statistical tests. Where a discrepancy between a sponsor analysis and a recalculation is flagged, the sponsor’s analysis takes precedence; no such discrepancy is flagged for this primary result.

The registry record does not report enough detail to independently reconstruct the stratified model, including its strata and implementation choices. The reported hazard ratio, interval, and p-value should be read as the sponsor’s posted analysis rather than as a result validated by the unadjusted re-calculation.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary composite endpoint and reports two secondary composite endpoints. It also reports an analysis for each using a stratified Cox proportional hazard model. However, the registry record does not report a complete statistical analysis plan, a hierarchy for testing the outcomes, or a method for controlling multiplicity. Without those details, the posted secondary p-values should not be interpreted as if they necessarily preserve a single overall error rate across all endpoint tests.

Multiplicity is a general statistical concern when many hypotheses are assessed. Repeated testing can increase the chance that one result appears statistically significant by chance, even when no corresponding effect exists. Prespecified testing sequences or adjustment methods can address this concern, but the registry record does not report whether either approach was used. This uncertainty is particularly relevant when interpreting secondary outcomes as confirmatory evidence.

The primary endpoint population is described as all subjects randomized to treatment. The registry does not specify in the available record how missing outcome data were handled, how censoring was defined, how protocol deviations affected inclusion, or whether any sensitivity analyses were performed. The treatment of missing data and censoring can affect time-to-event estimates; these details are therefore important to assess the robustness of the reported hazard ratio.

The record also does not report interim analyses, stopping boundaries, the original sample-size justification, or a detailed account of the analysis population used for the sponsor’s Cox model. These absences do not demonstrate that such procedures were not used; they mean the details are not reported in the registry record. The randomized population is specified for the primary endpoint, but more detailed population definitions for each analysis are not reported.

Independent clinical endpoint committee adjudication is reported for efficacy endpoints. That describes an outcome-review procedure, but it does not resolve the reporting gaps about missing data, multiplicity, censoring, or model diagnostics. These uncertainties should be kept separate from the estimates themselves: the posted values are clear, while the full analytical context needed to evaluate all assumptions is incomplete.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: chest pain (2.6%), angina pectoris (1.7%), corona virus infection (1.5%), non-cardiac chest pain (1.3%), pneumonia (1.3%).

The registry reports serious adverse events in 923 of 3076 participants in the placebo group and 900 of 3071 participants in the dalcetrapib group. Other adverse events were reported for 818 participants in the placebo group and 971 in the dalcetrapib group. Deaths are listed for 180 participants in the placebo group and 182 in the dalcetrapib group. These are posted counts; they are not, by themselves, adjusted comparisons or evidence about the cause of an event.

The registry lists chest pain at 2.6%, angina pectoris at 1.7%, corona virus infection at 1.5%, non-cardiac chest pain at 1.3%, pneumonia at 1.3%, and atrial fibrillation at 1.2% among the top serious adverse event terms. The record excerpt does not specify the arm-specific breakdown for these listed terms, so they should not be attributed to either group individually.

Adverse-event counts need context, including definitions, observation time, relatedness assessment, and completeness of reporting. Those details are not reported in the registry record. The figures describe the posted safety counts and should not be read as establishing that treatment caused or prevented any particular event.

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

The posted data describe a randomized comparison of dalcetrapib and placebo in participants recently hospitalized for acute coronary syndrome who had the specified genetic profile. For the primary composite, the registry reports a stratified Cox hazard ratio of 0.88, with a 95% confidence interval from 0.75 to 1.03 and p = 0.12. The unadjusted comparison of participant event proportions also has an interval that includes no difference. Taken together, these estimates leave uncertainty about the size and direction of the underlying difference.

The findings do not establish that the groups were identical. A confidence interval that includes the null value means the data do not rule out that value at the stated confidence level; it does not prove the absence of an effect. Conversely, a point estimate on one side of the null does not establish a difference when its uncertainty remains substantial. The reported p-value is not a measure of the probability that a treatment effect exists.

The primary endpoint is a composite of cardiovascular death, resuscitated cardiac arrest, non-fatal myocardial infarction, and non-fatal stroke. The overall result does not reveal the effect on each component separately. The two secondary composite outcomes add other events, but their posted analyses likewise do not establish a clear difference, and the registry record does not report a multiplicity procedure.

These findings apply to the trial’s selected, genetically defined population and the measured follow-up period, with median follow-up of 39.9 months. They do not directly answer questions about other populations, different treatment schedules, outcomes outside the composites, or longer-term results. The record describes the clinical outcomes observed and the analyses posted; it does not support a broader claim about treatment effects beyond those data.

18. Why This Trial Matters Statistically

This trial is statistically informative because it brings together randomization, a genetically defined eligibility group, an adjudicated composite endpoint, and a time-to-event analysis. Each feature shapes what the result can answer. Randomization supports a group comparison, genetic selection defines the population to which the result pertains, adjudication provides a specified process for evaluating efficacy events, and the Cox analysis incorporates event timing.

The primary result also illustrates why effect estimates and their precision need to be read together. The hazard ratio is 0.88, but its 95% confidence interval extends from 0.75 to 1.03 and includes 1.00. The unadjusted risk-difference interval also includes zero. A point estimate gives a concise direction and scale; its confidence interval shows how much uncertainty remains. Neither the point estimate nor the p-value alone captures the full statistical interpretation.

The distinction between an unadjusted re-calculation and a sponsor-reported model is another important lesson. Counts can be used to derive a simple comparison of observed proportions, while a time-to-event model uses timing and follow-up information. Similar-looking estimates can still represent different quantities and answer different statistical questions. A re-calculation is useful as a transparent check on posted counts, but it does not replace the reported model analysis.

The registry record also shows why reporting details matter. Information about multiplicity, missing data, censoring, model checks, and original design assumptions is needed to evaluate the analysis fully. When these details are not reported, conclusions should remain tied to the posted endpoint definitions and estimates rather than extending beyond them.

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 outcome is composite, so an overall result can conceal variation among its components. The registry record does not report component-specific primary event counts or treatment comparisons. It is therefore not possible to determine from the posted composite result which component contributed most or whether component results followed the overall pattern.

The trial population was selected based on recent acute coronary syndrome and a genetic profile, with genotype testing described as evaluating the AA genotype. This selection makes the question specific to that population. The findings should not automatically be generalized to people who do not meet those characteristics. The required randomization window was 4-12 weeks after the index event, which also defines the study context.

The registry provides a median follow-up duration of 39.9 months but does not report the distribution of follow-up, censoring details, or the handling of missing outcomes. The Cox model is reported as stratified, but the stratification factors and model diagnostics are not reported in the registry record. These gaps limit independent evaluation of the time-to-event analysis.

The registry does not report the full statistical analysis plan, multiplicity adjustment, interim analyses, or original sample-size justification. The sample-size illustrations based on observed effects are not substitutes for the trial’s original planning rationale. The primary analysis population is described as all randomized subjects, but additional details about analysis populations and protocol deviations are not reported.

Finally, the available safety summary gives arm-level counts for serious and other adverse events and deaths, plus selected serious event terms. It does not provide detailed attribution, timing, exposure-adjusted comparisons, or arm-specific counts for each listed term. These reporting limitations do not change the posted counts, but they constrain conclusions that can be drawn from them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effect of Dalcetrapib vs Placebo on CV Risk in a Genetically Defined Population With a Recent ACS — NCT02525939.
• Registry record last updated 2022-10-12; status last verified 2022-09.
• Results first posted 2022-10-12.
• 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

Dal-GenE was a completed, randomized, parallel-group Phase III study comparing once-daily dalcetrapib 600 mg with matching placebo in a genetically defined population recently hospitalized for acute coronary syndrome. The registry reports enrollment of 6147 and median follow-up of 39.9 months.

The primary endpoint was time to the first occurrence of cardiovascular death, resuscitated cardiac arrest, non-fatal myocardial infarction, or non-fatal stroke. The sponsor-reported stratified Cox analysis gave a hazard ratio of 0.88, with a 95% confidence interval from 0.75 to 1.03 and p = 0.12. The unadjusted event-count comparison also had a confidence interval including no difference.

The two posted secondary composites did not establish a clear between-group difference. Important details about multiplicity, missing data, model diagnostics, and the original design assumptions are not reported in the registry record.