Pemafibrate to Reduce Cardiovascular OutcoMes by Reducing Triglycerides IN patiENts With diabeTes (PROMINENT): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pemafibrate to Reduce Cardiovascular OutcoMes by Reducing Triglycerides IN patiENts With diabeTes (PROMINENT) (NCT03071692), a randomized phase 3 study. The primary outcome is Number of Participants With First Occurrence of 4-component Composite Primary Endpoint (Nonfatal MI, Nonfatal Ischemic Stroke, Coronary Revascularization, or CV Death).

2. Clinical Question

The registry record identifies the trial as PROMINENT and gives its formal title as “Pemafibrate to Reduce Cardiovascular OutcoMes by Reducing Triglycerides IN patiENts With diabeTes.” It records a Phase 3 study sponsored by Kowa Research Institute, Inc. These design details establish the intended comparison, but they do not by themselves establish the effectiveness of either treatment. The interpretation depends on the observed outcomes, the uncertainty around the comparison, and the completeness of the analysis information in the registry record.

3. Trial Design

PROMINENT is recorded as a randomized, quadruple-masked, parallel-group Phase 3 trial. Participants were assigned to pemafibrate or matching placebo, with both study tablets taken twice daily. The registry lists enrollment as 10544. The primary outcome population is identified as the intention-to-treat population, which generally refers to analyzing participants according to their randomized group; the detailed implementation of that population is not reported in the registry record.

The listed conditions are type 2 diabetes and dyslipidemia. The record identifies Kowa Research Institute, Inc. as sponsor and gives the study status as terminated. The recorded study start is 2017-03-23, and the primary completion date is 2022-07-27. The primary outcome timeframe is from baseline to a median of 3.3 years. The reason the study was terminated is not reported in the registry record, so the status alone does not establish why the trial ended or whether it ended as originally intended.

The primary endpoint is a time-to-first-event composite, while the posted primary outcome measure gives the number of participants with a first occurrence. Its components are nonfatal myocardial infarction, nonfatal ischemic stroke, coronary revascularization, and cardiovascular death. Each participant is counted once for this measure, even if additional events occur later. The sponsor's posted analysis expresses the group comparison as a hazard ratio. Details such as the randomization procedure, the exact meaning of each masking level, treatment adherence, follow-up procedures, and the statistical methods used for the sponsor's analysis are not reported in the registry record.

Several secondary outcomes are also registered, including other cardiovascular composites and outcomes involving heart failure, peripheral artery disease, and individual events. The record lists 20 posted secondary outcomes and 21 outcome measures overall. The available outcome information does not describe every component's event counts or provide a complete account of the analysis plan. Those omissions limit how much can be concluded about the wider set of trial questions.

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: Prior to treatment, participants attended a Prescreening Visit, a Screening/Enrollment Visit and a Placebo Run-In Period. Eligible subjects who were compliant with study treatment during the Placebo Run-In Period returned for the Randomization Visit, at which time they were randomly allocated to receive either pemafibrate or a matching placebo tablet.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intention to treat population (ITT)

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.

Population: The Intent to treat (ITT) population included all randomized subjects who received at least 1 dose of study treatment without GCP deviations.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With First Occurrence of 4-component Composite Primary Endpoint (Nonfatal MI, Nonfatal Ischemic Stroke, Coronary Revascularization, or CV Death), measured over From Baseline to a Median of 3.3 Years.

The primary endpoint counts participants who experienced a first occurrence of any of four events: nonfatal myocardial infarction, nonfatal ischemic stroke, coronary revascularization, or cardiovascular death. The registry's timeframe is from baseline to a median of 3.3 years, and the primary population is the intention-to-treat population. A participant is counted once for the endpoint even if more than one qualifying event occurs subsequently.

A composite endpoint combines several clinically defined outcomes into one measure. As a general statistical feature, this can capture a broader range of events and provide a single primary comparison. It also means that the overall result reflects the combined endpoint rather than each component separately. The components may differ in frequency or clinical importance, and a composite result alone does not show which component contributed most. Component-specific interpretation requires component-level results, which are not reported for the primary endpoint in the registry record.

The outcome description refers to first occurrence, making timing relevant to the trial's primary question about delaying an event. The sponsor reports a hazard ratio, a measure used for comparing event rates over follow-up in time-to-event analysis. The posted count comparison is a different summary: it describes the number of participants with an event during the recorded period. Neither summary, on its own, describes every aspect of event timing or the experience of participants who did not have a recorded event.

The reason for using this specific four-component endpoint, including any rationale for choosing the components or their weighting, is not reported in the registry record. The endpoint should therefore be read according to its stated definition rather than as a measure of every possible cardiovascular outcome.

7. Results Posted in the Registry

• Pemafibrate: 11.3% (590/5240) versus 10.8% (570/5257) on control; risk difference 0.4 percentage points (95% CI -0.8 to 1.6), risk ratio 1.04 (0.93–1.16); unadjusted two-proportion z-test p = 0.496.

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.

Number of Participants With First Occurrence of the 4-component Composite Secondary Endpoint (Nonfatal MI, Nonfatal Ischemic Stroke, Hospitalization for Unstable Angina Requiring Unplanned Coronary Revascularization, or CV 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:
  • Pemafibrate: 8.5% (447/5240) versus 8.1% (427/5257) on control; risk difference 0.4 percentage points (95% CI -0.6 to 1.5), risk ratio 1.05 (0.92–1.19); 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 Pemafibrate and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With First Occurrence of the 3-component Composite Endpoint (Nonfatal Myocardial Infarction, Nonfatal Ischemic Stroke, or 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:
  • Pemafibrate: 7.6% (396/5240) versus 7.3% (386/5257) on control; risk difference 0.2 percentage points (95% CI -0.8 to 1.2), risk ratio 1.03 (0.90–1.18); unadjusted two-proportion z-test p = 0.675.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pemafibrate and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With First Occurrence of Any Component of the Primary Endpoint or Hospitalization for 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:
  • Pemafibrate: 12.8% (670/5240) versus 12.3% (645/5257) on control; risk difference 0.5 percentage points (95% CI -0.7 to 1.8), risk ratio 1.04 (0.94–1.15); unadjusted two-proportion z-test p = 0.424.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pemafibrate and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary comparisons follow the same broad pattern as the primary result: their estimates are close to the null values, and the reported confidence intervals include the corresponding null values. The secondary endpoints cover related cardiovascular composites and outcomes that add hospitalization for heart failure or examine selected components. This overall pattern does not establish that every secondary outcome is identical between groups; rather, the estimates are uncertain and do not provide a clear separation from the null in the posted comparisons.

These secondary outcomes help describe related aspects of the trial question, but they do not replace the primary endpoint. Some use different composite definitions, and each can represent a distinct statistical question. A secondary result may be consistent with the primary result without independently confirming it, especially where outcome definitions overlap. The record lists 20 posted secondary outcomes, so the full set should be considered rather than selecting an isolated result.

Unadjusted secondary results carry less weight when the multiplicity plan is not reported. As a general statistical concern, examining many outcomes creates more opportunities for a chance finding. Without a reported adjustment strategy or hierarchy of testing, an unadjusted result should be viewed as exploratory rather than treated as definitive evidence. The registry record does not report a complete multiplicity procedure, and no such procedure should be assumed.

Only the secondary comparisons with detailed outcome and analysis information in the record can be interpreted at that level. The record's broader list of secondary outcomes does not, by itself, provide numerical results for every endpoint. A comprehensive assessment of the secondary findings would require their definitions, estimates, uncertainty intervals, and analysis methods, along with the planned approach to multiple comparisons.

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

• Number of Participants With First Occurrence of the 4-component Composite Secondary Endpoint (Nonfatal MI, Nonfatal Ischemic Stroke, Hospitalization for Unstable Angina Requiring Unplanned Coronary Revascularization, or CV Death)
• Number of Participants With First Occurrence of the 3-component Composite Endpoint (Nonfatal Myocardial Infarction, Nonfatal Ischemic Stroke, or Cardiovascular Death)
• Number of Participants With First Occurrence of Any Component of the Primary Endpoint or Hospitalization for Heart Failure
• Number of Participants With Occurrence of Any Component of the Primary Endpoint or All-Cause Mortality
• Total Number of Events of the 4-component Composite Primary Endpoint
• Number of Participants With First Occurrence of Any New or Worsening Peripheral Artery Disease (PAD)
• Number of Participants With First Occurrence of Nonfatal Myocardial Infarction
• Number of Participants With First Occurrence of Nonfatal Ischemic Stroke

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference describe?

A risk difference compares the proportion of participants with an event in one group with the proportion in another group. A value of zero represents equal proportions. For the primary endpoint, the unadjusted recalculation gives a risk difference of 0.004 for pemafibrate relative to placebo, with a 95% confidence interval from -0.008 to 0.016. The estimate is based on the posted event counts and group sizes. It is not an adjusted estimate and does not account for time to event in the way a time-to-event model does.

As a general statistical explanation, an absolute difference can be easier to relate to the observed group proportions than a relative measure. It still depends on the endpoint definition, follow-up period, and the enrolled population. It should not be treated as a guarantee about an individual participant's outcome.

What does the hazard ratio describe?

The sponsor reports a hazard ratio of 1.03 for the primary endpoint, with a 95% confidence interval from 0.92 to 1.16. In general, a hazard ratio compares the event rates over time between groups, subject to the assumptions of the analysis. A value of 1 represents equal hazards under that measure. A hazard ratio is not the same as a ratio of the total numbers of participants with events, and it is not an absolute difference in event probability.

The sponsor's method and model details are not reported in the registry record. In particular, the record does not specify the model form, covariate adjustment, or how censoring was handled. The hazard ratio should therefore be reported as the sponsor's posted analysis, without attributing unreported methods to it.

How should confidence intervals be read?

A confidence interval describes the uncertainty associated with an estimate under the statistical procedure used. As a general explanation, a 95% confidence interval is produced by a method that, under its assumptions and repeated use, would cover the underlying parameter in 95% of such intervals. It is not a statement that there is a 95% probability that the fixed parameter lies within this particular interval.

For the risk difference, zero is the null value of no difference; for the hazard ratio, the corresponding null value is 1. The posted intervals include their respective null values. This indicates that the reported estimates do not sharply distinguish the comparison from the null at the level conveyed by those intervals. It does not establish equivalence or prove that any possible difference is absent. Equivalence would require a prespecified margin and an analysis designed to evaluate that question; such a margin is not reported in the registry record.

What does the unadjusted p-value add?

The recalculated p-value for the primary risk difference is 0.496. A p-value measures how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions held. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. This p-value is unadjusted and comes from the simple recalculation, not the sponsor's reported time-to-event analysis. The registry record does not report a p-value for the sponsor's hazard ratio.

When many outcomes are examined, unadjusted p-values require particular caution because multiple opportunities for apparently unusual results can arise. The registry lists multiple secondary outcomes, but the multiplicity plan is not reported. Accordingly, secondary comparisons should not be read as if a single, prespecified test had been performed.

Why can dispersion matter in other outcome types?

General statistical context: for count outcomes, the variability can be larger than a simple model assumes. Over-dispersion means the observed variation exceeds that model's expectation; if not addressed, standard errors and confidence intervals may be too small. The primary outcome posted is a count of participants with an event, rather than a count of repeated events per person. The record describes a separate secondary outcome for total events, but the detailed statistical approach for that outcome is not reported in the registry record. No over-dispersion method should be attributed to the trial from the available information.

The registry record also does not report the original sample-size justification, the planned interim analyses, or a detailed statistical analysis plan. Those details matter for interpreting how the study was designed to answer its question and how outcome analyses were selected. They cannot be inferred from the enrollment number or the posted estimates.

11. Confidence Intervals and Precision

The primary endpoint has a sponsor-reported hazard ratio of 1.03 and a 95% confidence interval from 0.92 to 1.16. The interval extends below and above 1, the null value for a hazard ratio. This range indicates uncertainty about the direction and magnitude of the time-to-event comparison. The point estimate alone should not be treated as the complete result: the interval conveys that the data are compatible with a range of hazard-ratio values around that estimate.

The unadjusted recalculated risk difference is 0.004, with a 95% confidence interval from -0.008 to 0.016. This interval includes zero and spans negative and positive values. In general, the risk-difference interval represents uncertainty on an absolute scale, while the sponsor's hazard-ratio interval represents uncertainty on a relative time-to-event scale. Their widths and values therefore cannot be compared as though they were the same measure.

The sponsor-reported interval and recalculated interval are both relevant, but they arise from different forms of comparison. The sponsor's analysis uses a hazard ratio; the recalculation uses posted event counts and is unadjusted. The sponsor's model details are not reported in the registry record. The recalculated interval should not be taken as a replacement for the sponsor analysis, and neither interval establishes exact equality between groups.

Precision is also limited by what the record reports. It does not provide component-level primary estimates, the sponsor analysis p-value, or enough detail to assess all modeling and missing-data assumptions. The interval gives a statistical range under its analysis procedure, not a complete account of uncertainty from trial conduct, measurement, or generalizability. No clinically important difference threshold is reported, so the interval cannot be classified against such a threshold.

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 for the primary endpoint are participants per arm, not total events. They are illustrations based on the observed effect and are not the trial's original sample-size justification. The listed assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and detection of the stated fraction of the observed effect. The original design assumptions are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 88,799 participants per arm for 80% power and 118,876 participants per arm for 90% power. For planning at 75% of the observed effect, it gives 157,213 participants per arm for 80% power and 210,463 participants per arm for 90% power. For planning at 50% of the observed effect, it gives 352,261 participants per arm for 80% power and 471,577 participants per arm for 90% power.

In plain terms, the 80% power column describes the planning sample size that, under the stated assumptions, would give an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column expresses the corresponding planning target for a 90% chance. These are design illustrations, not a statement about the chance that the trial result is correct. Smaller target effects require more participants because they are harder to distinguish from random variation. This is not observed power.

The figures depend on the particular endpoint and observed effect used to construct the illustration. They should not be interpreted as recommendations for a future study without considering its own design, endpoint, follow-up, and assumptions. The registry record does not report the sample-size calculation used when PROMINENT was planned, so these illustrations cannot establish whether the trial met its original target or how that target was selected.

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 = 0.108; treatment proportion p₁ = 0.113; average p̄ = 0.111.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4434 = 0.8690.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4434 = 0.3732.
4. n = (0.8690 + 0.3732)² / (0.0042)² = 88,798.6, rounded up to 88,799 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 <- 0.108426859425528                          # control proportion
p1 <- 0.112595419847328                          # 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(3071692)
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 = 88,799 (80% power), 118,876 (90% power)
 75% of observed effect: n per arm = 157,213 (80% power), 210,463 (90% power)
 50% of observed effect: n per arm = 352,261 (80% power), 471,577 (90% power)
power.prop.test: 88798.6 
Simulated power at n = 88,799 per arm: 0.797 (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 sponsor's primary analysis reports a hazard ratio of 1.03, with a 95% confidence interval from 0.92 to 1.16. This is a time-to-event comparison. The registry record does not report the sponsor analysis method or a p-value. The hazard-ratio interval includes 1, its null value.

The simple recalculation from the posted participant counts gives an unadjusted risk difference of 0.004, with a 95% confidence interval from -0.008 to 0.016 and an unadjusted p-value of 0.496. This calculation compares event proportions and does not reproduce the sponsor's time-to-event analysis. The estimates are related in that they compare the same randomized groups and primary endpoint, but they use different statistical summaries and should not be substituted for one another.

The recalculation is a check based on posted summary counts. It does not incorporate any unreported adjustment, event timing, censoring, or model specification. The sponsor's own analysis takes precedence for the trial's reported time-to-event result. Because the sponsor's model details are not reported in the registry record, the difference between the measures should be described rather than attributed to a particular modeling choice.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists 20 posted secondary outcomes and 23 analyses, but it does not report how multiplicity was handled. Multiplicity concerns arise when several outcomes or comparisons are tested: even if each test uses a conventional threshold, the chance of at least one apparently unusual result can increase across a collection of tests. As general statistical context, adjustment methods or a prespecified testing hierarchy can help control that issue. The record does not identify such a method or hierarchy, so secondary findings should be interpreted cautiously and not treated as confirmatory solely on the basis of unadjusted comparisons.

The primary outcome population is identified as intention to treat. The registry record does not describe the operational definition used for that population, including how participants with missing outcome data or deviations from assigned treatment were handled. It also does not report a missing-data strategy, censoring rules, or sensitivity analyses. Those details are important for judging how incomplete follow-up may affect a time-to-event analysis and how missing outcome information may affect participant counts.

The sponsor reports a hazard ratio, but the specific statistical model, adjustment variables, assumptions, and analysis implementation are not reported in the registry record. The recalculated risk difference is unadjusted and uses the posted summary counts; it does not fill these gaps. Results for analysis populations other than the named intention-to-treat population are not reported in the record.

The record also does not report the original sample-size justification, planned interim analyses, or a complete statistical analysis plan. It is therefore not possible to establish from the posted information whether the reported analyses followed a particular prespecified sequence, whether interim monitoring affected the study, or what rules governed data inclusion. These are missing details, not evidence that a particular method was or was not used.

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: angina unstable (1.8%), acute myocardial infarction (1.8%), covid-19 pneumonia (1.8%), pneumonia (1.6%), cardiac failure (1.6%).

The registry reports serious adverse event figures for 5264 participants at risk in the pemafibrate group, with 1715 affected, and 5274 participants at risk in the placebo group, with 1663 affected. It also reports other adverse event figures for 5264 participants at risk in the pemafibrate group, with 2817 affected, and 5274 at risk in the placebo group, with 2883 affected. Death counts are recorded as 308 and 310, respectively. These are the registry's reported counts; no further rate calculation is made.

The listed serious adverse event terms include unstable angina at 1.8%, acute myocardial infarction at 1.8%, COVID-19 pneumonia at 1.8%, pneumonia at 1.6%, cardiac failure at 1.6%, and atrial fibrillation at 1.4%. The registry record does not provide the detailed definitions, event-level timing, or attribution methods needed to assess these terms beyond their listing.

Adverse event counts are descriptive and do not alone establish that an event was caused by study treatment. The registry record does not provide enough information to evaluate all safety analyses, severity grading, exposure duration, or statistical comparisons. The reported figures should be read as recorded safety summaries rather than as a causal conclusion.

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

The result describes a randomized comparison of pemafibrate and placebo for a specific composite cardiovascular endpoint among participants with type 2 diabetes and dyslipidemia. During follow-up from baseline to a median of 3.3 years, the posted counts show a first event in 590 of 5240 participants assigned to pemafibrate and 570 of 5257 assigned to placebo. The sponsor's hazard-ratio estimate is 1.03, with a 95% confidence interval from 0.92 to 1.16.

The estimates and confidence intervals do not show a clear separation from the null values for the reported measures. That does not prove the groups had identical outcomes, and it does not establish that every clinically relevant difference is excluded. The intervals include a range of possible values, and the record does not identify a threshold for a clinically important difference. The result should therefore be read as an estimate with uncertainty rather than a binary verdict.

The endpoint combines four events. The overall result cannot identify which component contributed most, and the primary component-specific estimates are not reported in the registry record. It also does not answer questions about outcomes outside the registered endpoint or beyond the recorded follow-up. The secondary outcomes address additional questions, but their multiplicity plan is not reported.

These results are not medical advice and do not determine an individual's treatment choice. They do not establish why the trial was terminated, because the reason is not reported in the registry record. Nor do they automatically apply to populations that differ from those enrolled. The record gives the study conditions but does not provide all eligibility criteria or participant characteristics needed to assess the boundaries of generalization.

18. Why This Trial Matters Statistically

PROMINENT illustrates why a clinical trial result should be read through both its design and its uncertainty. Randomization and a matching placebo establish a comparative framework, while the quadruple-masked, parallel-group designation describes additional recorded design features. The primary endpoint is a composite of four cardiovascular events and is defined by first occurrence, so its meaning depends on both the component definitions and the rule that a participant is counted once.

The trial also illustrates the distinction between a sponsor-reported time-to-event analysis and a simple recalculation from participant counts. The sponsor's hazard ratio summarizes event rates over time, while the recalculated risk difference compares the recorded proportions with events. Reporting the two measures separately makes their different scales and assumptions visible. The sponsor analysis remains the principal posted time-to-event result; the recalculation is a complementary, unadjusted summary.

Precision matters as much as the point estimate. The confidence intervals include the null values, leaving uncertainty about the size and direction of the comparison. This does not prove equality, and the registry record does not report a clinically important difference threshold that could further frame the interval.

The registered secondary outcomes and safety summaries broaden the questions readers may ask, but the multiplicity plan and several analysis details are not reported. That makes careful restraint important: individual secondary findings cannot be elevated beyond the evidence and context recorded. Together, these features show why interpretation requires attention to endpoint construction, analysis scale, uncertainty, and the completeness of registry information.

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.

Several limitations are specific to the information recorded for this trial. The sponsor's method for estimating the primary hazard ratio is not reported, including model specification, adjustment variables, and handling of censoring. The sponsor analysis also has no posted p-value in the registry record. The unadjusted recalculation from participant counts is not a substitute for those missing methodological details.

The primary endpoint combines nonfatal myocardial infarction, nonfatal ischemic stroke, coronary revascularization, and cardiovascular death. Component-level primary event results are not reported, limiting interpretation of how the composite was formed. The rationale for selecting these components and any weighting or hierarchy among them are also not reported.

The registry identifies the intention-to-treat population but does not describe the operational analysis rules, missing-data methods, or sensitivity analyses. It does not report the original sample-size justification, planned interim analyses, or a detailed statistical analysis plan. The reason for the terminated status is not reported, so that status cannot be used to infer why the study ended.

Although many secondary outcomes are listed, the multiplicity strategy is not reported. This limits the confirmatory interpretation of unadjusted secondary comparisons. Finally, detailed eligibility criteria and participant characteristics are not included in the recorded details used for these summaries, constraining assessment of how closely the trial population represents any particular group outside the stated conditions.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Pemafibrate to Reduce Cardiovascular OutcoMes by Reducing Triglycerides IN patiENts With diabeTes (PROMINENT) — NCT03071692.
• Registry record last updated 2025-09-25; status last verified 2025-09.
• Results first posted 2025-09-25.
• 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

The registry record identifies PROMINENT as a randomized, quadruple-masked, parallel-group Phase 3 trial of pemafibrate versus matching placebo in participants with type 2 diabetes and dyslipidemia. It records enrollment of 10544, sponsorship by Kowa Research Institute, Inc., and a terminated status. The primary outcome is first occurrence of nonfatal myocardial infarction, nonfatal ischemic stroke, coronary revascularization, or cardiovascular death, assessed from baseline to a median of 3.3 years in the intention-to-treat population.

The posted primary counts are 590 of 5240 for pemafibrate and 570 of 5257 for placebo. The sponsor reports a hazard ratio of 1.03 (95% CI 0.92 to 1.16). An unadjusted recalculation gives a risk difference of 0.004 (95% CI -0.008 to 0.016; p = 0.496). The registry record does not report the sponsor's detailed statistical method, missing-data approach, multiplicity plan, original sample-size justification, or reason for termination.