Efficacy and Safety of Finerenone in Subjects With Type 2 Diabetes Mellitus and Diabetic Kidney Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Finerenone in Subjects With Type 2 Diabetes Mellitus and Diabetic Kidney Disease (NCT02540993), a randomized phase 3 study. The primary outcome is The First Occurrence of the Composite Endpoint of Onset of Kidney Failure, a Sustained Decrease of eGFR ≥40% From Baseline Over at Least 4 Weeks, or Renal Death.

2. Clinical Question

3. Trial Design

This was a randomized, double-blind, placebo-controlled, parallel-group, multicenter, event-driven Phase 3 study sponsored by Bayer. The registry lists quadruple masking. A total enrollment of 5734 is recorded, with 2833 participants in the finerenone group and 2841 in the placebo group for the primary endpoint analysis. The study is marked completed. Its recorded start date is 2015-09-17, and its primary completion date is 2020-04-14.

Both groups received standard of care therapy. The intervention group received finerenone 10 mg or 20 mg once daily, while the comparator group received matching placebo once daily. The registry does not report the allocation ratio or the method used to determine which finerenone dose an individual received. It also does not report the original sample-size justification or the detailed operational definition of event-driven follow-up.

The primary outcome was a time-to-first-event composite of kidney failure, a sustained eGFR decrease of at least 40% from baseline over at least 4 weeks, or renal death. Average follow-up for the primary outcome was 32 months. The registry describes the primary population as the full analysis set and reports both participant event counts and a log-rank analysis expressed as a hazard ratio.

Posted secondary outcomes include a cardiovascular composite, all-cause mortality, all-cause hospitalization, change in urinary albumin-to-creatinine ratio at Month 4, and a further kidney composite using a sustained eGFR decrease of at least 57%. Results are posted for only some of these outcomes; the results for outcomes without posted estimates are not reported in the registry record. The study’s detailed protocol, including its full statistical analysis plan, is 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: Overall, 13911 participants were screened. Of them, 8177 participants were screening failures and 5734 participants were randomized to study treatment. 60 participants were prospectively excluded from the analyses because of Good Clinical Practice (GCP) violations, resulting in 5674 participants in the full analysis set (FAS). 16 participants did not take any study drug, resulting in 5658 participants who received study treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set

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: Full analysis set (FAS): the FAS comprised all randomized participants (except those with critical GCP violations)

6. Primary Endpoint

The registry lists the primary outcome as The First Occurrence of the Composite Endpoint of Onset of Kidney Failure, a Sustained Decrease of eGFR ≥40% From Baseline Over at Least 4 Weeks, or Renal Death, measured over From randomization up until the first occurrence of the primary renal composite endpoint, or censoring at the end of the study, with an average follow-up time of 32 months.

The primary endpoint records the first occurrence of any of three events: onset of kidney failure, a sustained decrease in estimated glomerular filtration rate of at least 40% from baseline over at least 4 weeks, or renal death. The registry reports the number of participants experiencing the composite and describes follow-up from randomization to the first event or censoring at study end, with an average follow-up time of 32 months.

A composite endpoint can capture more than one way that the disease process may progress. In this case, the events span kidney failure, a substantial sustained change in eGFR, and renal death. The composite also makes the first qualifying event the analysis focus; it does not, by itself, show how each component contributed to the overall result. Component-specific primary outcome counts are not reported in the registry record.

For a time-to-event outcome, the timing of events and the duration of observed follow-up matter. A participant who has not experienced the endpoint by the end of observed follow-up is censored rather than automatically counted as having an event. The registry’s reported log-rank analysis summarizes the comparison over follow-up as a hazard ratio. The participant counts offer a separate descriptive view of how many people had an event, but do not preserve all of the timing information used in the time-to-event analysis.

7. Results Posted in the Registry

• Finerenone: 17.8% (504/2833) versus 21.1% (600/2841) on control; risk difference -3.3 percentage points (95% CI -5.4 to -1.3), risk ratio 0.84 (0.76–0.94); unadjusted two-proportion z-test p = 0.002.

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.

The First Occurrence of the Composite Endpoint of Cardiovascular Death, Non-fatal Myocardial Infarction, Non-fatal Stroke, 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:
  • Finerenone: 13.0% (367/2833) versus 14.8% (420/2841) on control; risk difference -1.8 percentage points (95% CI -3.6 to -0.0), risk ratio 0.88 (0.77–1.00); unadjusted two-proportion z-test p = 0.046.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Finerenone 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:
  • Finerenone: 7.7% (219/2833) versus 8.6% (244/2841) on control; risk difference -0.9 percentage points (95% CI -2.3 to 0.6), risk ratio 0.90 (0.76–1.07); unadjusted two-proportion z-test p = 0.238.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Finerenone and the control. The interval gives the range of effects that remain compatible with the data.

All-cause Hospitalization

• 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:
  • Finerenone: 44.6% (1263/2833) versus 46.5% (1321/2841) on control; risk difference -1.9 percentage points (95% CI -4.5 to 0.7), risk ratio 0.96 (0.91–1.01); unadjusted two-proportion z-test p = 0.147.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Finerenone and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results cover a cardiovascular composite, all-cause mortality, and all-cause hospitalization. For these outcomes, the registry reports time-to-event estimates as well as participant event counts. The estimates do not all have the same degree of statistical precision, and the intervals for mortality and hospitalization include the no-difference value. Results for the Month 4 UACR change and the further kidney composite are not reported in the registry record, despite their listing as secondary outcomes.

The secondary findings provide context around the primary renal result, but they do not independently establish or negate it. The cardiovascular endpoint is a distinct composite, while mortality and hospitalization are separate outcomes. Their event definitions, frequencies, and statistical uncertainties differ from those of the primary renal endpoint. The secondary results should therefore be considered outcome by outcome rather than treated as a single overall confirmation.

Unadjusted secondary p values carry less inferential weight when several outcomes are tested because the chance of at least one apparently notable result can increase across multiple comparisons. A multiplicity procedure or prespecified testing hierarchy can address that issue, but neither is reported in the registry record. It is consequently not possible to determine from the posted record whether the secondary findings were protected by a formal family-wise testing strategy, or how their p values were intended to be interpreted.

The secondary pattern is best understood as descriptive evidence alongside the primary analysis, with uncertainty and multiplicity kept in view. The registry does not report all listed secondary outcomes, nor does it provide component-level results for the primary composite. No single secondary estimate should be used to infer effects on outcomes that were not reported or to replace the primary endpoint analysis.

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

• The First Occurrence of the Composite Endpoint of Cardiovascular Death, Non-fatal Myocardial Infarction, Non-fatal Stroke, or Hospitalization for Heart Failure
• All-cause Mortality
• All-cause Hospitalization
• Change in Urinary Albumin-to-creatinine Ratio (UACR) From Baseline to Month 4
• The First Occurrence of the Composite Endpoint of Onset of Kidney Failure, a Sustained Decrease in eGFR of ≥57% From Baseline Over at Least 4 Weeks, or Renal Death

9. Statistical Interpretation

10. Statistical Methods Explained

What does the time-to-event analysis use?

The primary outcome is defined by the first qualifying event after randomization. A time-to-event analysis uses both whether an event occurred and the time until it occurred. Participants who remain under observation without a recorded event until study end are censored at that point. Censoring preserves the information that an event had not been observed by the last recorded follow-up, without treating that participant as if they had an event or as if they had complete follow-up indefinitely.

The registry reports a log-rank analysis and expresses its result as a hazard ratio. A hazard ratio compares event rates over follow-up between groups, rather than simply comparing the final proportions with an event. A value below 1 indicates a lower estimated event rate over follow-up in the finerenone group relative to placebo in this analysis. The registry reports the primary hazard ratio as 0.825, with a 95% confidence interval from 0.732 to 0.928 and p = 0.001. The full model specification and any covariate adjustment are not reported in the registry record.

How does the recalculation differ?

The recalculated comparison uses the posted event counts and group sizes as an unadjusted binary comparison. It estimates the difference between the observed event proportions: -0.033, with a 95% confidence interval from -0.054 to -0.013 and p = 0.002. A risk difference is expressed on the absolute probability scale. Its negative value means the observed proportion with an event was lower in the finerenone group in this calculation.

This recalculation does not use the timing of events or the censoring information that the time-to-event analysis uses. It is therefore a simple complementary description of the posted counts, not a replacement for the registry’s sponsor-reported primary analysis. The confidence interval for a risk difference is compared with 0, the value that represents no absolute difference. For a hazard ratio, the corresponding no-difference value is 1.

What do confidence intervals and p values contribute?

A confidence interval describes the range of effect estimates compatible with the data under the method’s assumptions and gives information about precision. It does not guarantee that the true effect lies in that range, nor does it account for limitations that are not represented in the analysis. The primary hazard-ratio interval excludes 1, while the recalculated risk-difference interval excludes 0. The reported p values describe how compatible the data are with a specified no-difference null hypothesis under the respective statistical procedure; they do not measure the probability that a treatment effect is true.

The registry labels the sponsor’s primary analysis as a superiority analysis. The recalculated p value is unadjusted. The original significance threshold, any adjustment for multiple endpoints, and the planned hierarchy among outcomes are not reported in the registry record. Consequently, the primary p value can be described as reported, but the status of secondary p values within a family of tests cannot be determined from this record alone.

Why are composite outcomes interpreted cautiously?

A composite combines multiple event types into one endpoint. It can increase the number of observed outcomes and capture several forms of disease progression, but its overall estimate does not reveal which component contributed most. Here, the registry posts the primary composite count and analysis but does not report separate counts or treatment estimates for kidney failure, sustained eGFR decline, and renal death. No conclusion about the separate components can be drawn from the overall composite estimate alone.

In general, the components of a composite may differ in frequency and clinical meaning. A composite result therefore needs to be read alongside component-level results when those are available. Component-level primary results are not reported in the registry record. The endpoint also uses time to first occurrence, so later qualifying events in a participant do not contribute as additional primary events in the reported first-event endpoint.

What is the role of randomization and masking?

Randomization is intended to make treatment groups comparable on average at the start of a trial, including for factors that were not measured. That supports a causal comparison when the randomized groups are analyzed appropriately, though it does not eliminate uncertainty or guarantee balance on every characteristic. The registry identifies the study as randomized and parallel-group. It lists double-blind design and quadruple masking, but does not detail which roles were masked or how masking was maintained.

The registry identifies the primary analysis population as the full analysis set. The exact inclusion rules defining that set, and whether they correspond to a particular intention-to-treat convention, are not reported in the registry record. The analysis population matters because exclusions after randomization can affect how closely an estimate represents the randomized comparison.

What cannot be reconstructed from the record?

The record does not report the complete statistical analysis plan, the original sample-size justification, details of any interim analyses, the handling of missing outcome data, or the model specification beyond the named log-rank method and hazard-ratio parameter. These omissions limit independent assessment of analysis choices. They do not change the values reported, but they mean that important design and analysis decisions cannot be confirmed from the registry record alone.

11. Confidence Intervals and Precision

Precision concerns the range of effect sizes compatible with the observed data under a specified analysis. For the primary time-to-event result, the hazard ratio is 0.825 and the 95% confidence interval is 0.732 to 0.928. The interval lies below the no-difference value of 1. This is the uncertainty range reported for the sponsor’s primary analysis, not a guarantee about the true effect.

The unadjusted risk-difference recalculation is -0.033, with a 95% confidence interval from -0.054 to -0.013. Its interval lies below the no-difference value of 0. The risk-difference interval reflects uncertainty for the comparison of the posted event proportions; it does not incorporate the time-to-event information used by the sponsor’s analysis. The two intervals use different effect measures and should not be compared as if they described exactly the same estimand.

Confidence intervals are useful because they show more than whether a p value crosses a threshold: they show a range of effect estimates that remain compatible with the data and method. Narrower intervals generally indicate greater precision, while wider intervals indicate greater uncertainty. Precision is distinct from clinical importance, and the registry does not supply a threshold for interpreting the clinical importance of these effect sizes.

For the posted secondary time-to-event estimates, the confidence intervals vary in relation to 1. The cardiovascular composite interval is 0.747 to 0.989; the all-cause mortality interval is 0.746 to 1.075; and the all-cause hospitalization interval is 0.876 to 1.022. These intervals convey uncertainty for their respective analyses, but their inferential weight also depends on the unreported multiplicity plan. The registry record does not report confidence intervals for the separate primary endpoint components.

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 posted planning figures are illustrations based on the observed effect, not the trial’s original design calculations. For the binary event outcomes used in these planning rows, the figures are participants per arm. The general planning description distinguishes these from time-to-event planning, for which entries would be total events; the posted primary and secondary planning figures are stated as participants per arm.

The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect. The rows therefore describe planning for 100%, 75%, or 50% of the observed effect, rather than an alternative set of observed trial results. For example, the posted primary-outcome figures are 2,219 participants per arm for 80% power and 2,970 participants per arm for 90% power when planning for 100% of the observed effect. The corresponding figures for planning for 75% of the observed effect are 4,009 and 5,366 participants per arm; for 50%, they are 9,162 and 12,265 participants per arm.

The 80% power column describes a planning target: under the stated assumptions and if the assumed effect were the true effect, the design would have an 80% chance of detecting an effect at the specified significance level. The 90% column uses a higher chance of detection as its target. Smaller effects are harder to distinguish from random variation, so planning for a smaller effect requires more participants per arm. These figures are not observed power and do not describe the probability that the trial’s result is correct.

The trial’s own original sample-size assumptions and justification are not reported in the registry record. These planning figures should therefore be read as separate illustrations, not as evidence that the trial was designed around the displayed assumptions.

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 = 0.211; treatment proportion p₁ = 0.178; average p̄ = 0.195.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5598 = 1.0972.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5593 = 0.4707.
4. n = (1.0972 + 0.4707)² / (-0.0333)² = 2,218.4, rounded up to 2,219 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 <- 0.211193241816262                          # control proportion
p1 <- 0.177903282739146                          # 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(2540993)
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 = 2,219 (80% power), 2,970 (90% power)
 75% of observed effect: n per arm = 4,009 (80% power), 5,366 (90% power)
 50% of observed effect: n per arm = 9,162 (80% power), 12,265 (90% power)
power.prop.test: 2218.4 
Simulated power at n = 2,219 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-reported primary result is a log-rank time-to-event analysis with hazard ratio 0.825, 95% confidence interval from 0.732 to 0.928, and p = 0.001. It uses the timing of the first qualifying event and the observed follow-up, including censoring. This is the registry’s reported primary analysis and takes precedence as the trial’s own analysis.

The recalculated result uses the posted counts only: 504 events among 2833 participants receiving finerenone and 600 among 2841 receiving placebo. The unadjusted risk difference is -0.033, with a 95% confidence interval from -0.054 to -0.013 and p = 0.002. It is a simple comparison of event proportions and does not reproduce the time-to-event analysis.

The two analyses are not directly interchangeable because they estimate different quantities using different information. Their directions are consistent: both estimates favor a lower observed event occurrence in the finerenone group. The registry’s discrepancy flag is false, so no disagreement between the sponsor result and the recalculation is identified. The recalculation is a supplementary check on the posted counts, not a correction to the sponsor’s reported analysis.

The record does not report enough detail to reproduce the sponsor’s full analysis independently, including its complete model specification and handling of all analysis details. The reported hazard ratio, confidence interval, and p value can be described as registry results, but the underlying analysis cannot be fully reconstructed from the posted information alone.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates multiple outcomes, comparisons, time points, or analysis populations. If each is tested separately, the chance of finding at least one apparently strong result can rise. Statistical plans often address this through a testing hierarchy, adjusted thresholds, or other procedures. The registry lists several secondary outcomes and reports analyses for some of them, but the multiplicity plan is not reported in the registry record. The posted secondary p values should therefore not be assumed to have been adjusted or to share a particular confirmatory status.

The primary result is identified as a superiority analysis, and the sponsor reports p = 0.001. The registry also provides an unadjusted recalculated p value for the participant-count comparison. The original significance threshold and any rules governing the relationship between primary and secondary testing are not reported in the registry record. The planning illustration’s two-sided significance level of 0.05 is an assumption for those calculations, not evidence of the trial’s original testing plan.

Missing-data methods are also important. The record describes censoring at study end for the primary time-to-event outcome, but the detailed rules for censoring, loss to follow-up, missing endpoint information, and sensitivity analyses are not reported in the registry record. It is not possible to determine from the posted information how incomplete observations were handled beyond the stated endpoint timeframe.

The primary population is described as the full analysis set. The record does not define its membership in sufficient detail to verify the exact analysis population or how protocol deviations and post-randomization exclusions were treated. Interim analyses, stopping rules, and the complete statistical analysis plan are likewise not reported in the registry record. These omissions limit evaluation of prespecification, multiplicity control, missing-data robustness, and the exact population represented by the estimates. They do not establish that any 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: pneumonia (3.6%), acute kidney injury (2.0%), hyperkalaemia (1.5%), hypoglycaemia (1.1%), cellulitis (0.9%).

The registry lists serious adverse events affecting 902 of 2827 participants in the finerenone group and 971 of 2831 in the placebo group. Other adverse events are listed for 1602 of 2827 participants receiving finerenone and 1584 of 2831 receiving placebo. The listed death counts are 222 and 250, respectively. These are registry counts with their recorded denominators; they are not adjusted comparisons, and the record does not describe a statistical test for these safety figures.

The registry also lists the following serious adverse event terms and percentages: pneumonia, 3.6%; acute kidney injury, 2.0%; hyperkalaemia, 1.5%; hypoglycaemia, 1.1%; cellulitis, 0.9%; and urinary tract infection, 0.8%. The listed terms are not presented with arm-specific counts in the record, so they should not be assigned to one treatment group or interpreted as comparative rates.

Safety counts describe events recorded over the study, but the registry excerpt does not provide details such as event timing, duration, seriousness criteria, exposure-adjusted rates, or a causal assessment for individual events. Counts alone do not establish why an event occurred or whether observed differences reflect treatment, chance, or other factors. The figures should be read as descriptive registry data, not as a complete safety evaluation.

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

The primary result describes a randomized comparison of finerenone plus standard of care with placebo plus standard of care in the enrolled study population. The sponsor-reported time-to-event analysis estimated a hazard ratio of 0.825 for the first occurrence of the renal composite, with a 95% confidence interval from 0.732 to 0.928 and p = 0.001. The posted participant counts and the unadjusted recalculation point in the same direction, while answering a different statistical question.

The estimate concerns a composite of kidney failure, sustained eGFR decline of at least 40% from baseline over at least 4 weeks, or renal death. It does not show which component was most influential, because separate component results are not reported in the registry record. Nor does an average follow-up time of 32 months establish what happens beyond the observed study period.

A hazard ratio is a relative measure over follow-up, not a statement that every participant experienced the same change in risk. The confidence interval expresses statistical uncertainty under the analysis method; it does not capture every source of uncertainty, such as limitations in reporting, missing-data handling, or applicability to populations not represented in the study. The record does not report subgroup results that would support conclusions for particular participant characteristics.

The findings also do not settle the interpretation of every secondary outcome. Several secondary analyses are posted, but the testing hierarchy and multiplicity adjustment are not reported, and some listed secondary outcomes have no posted results. The registry’s safety counts are descriptive and do not by themselves establish causation or comparative safety.

Accordingly, the posted data support a description of the primary trial result and its statistical precision, not a universal conclusion about all patients, all outcomes, or longer-term effects. The result should be understood within the randomized comparison, endpoint definition, analysis population, and follow-up recorded for this study.

18. Why This Trial Matters Statistically

This trial illustrates why the choice of endpoint analysis matters in clinical research. The primary outcome is time to the first event in a composite, so the reported log-rank hazard ratio uses event timing and follow-up rather than only the final proportion of participants with an event. Comparing that result with the unadjusted risk-difference recalculation shows how the same posted counts can be described on a different scale, while also clarifying that the two analyses are not interchangeable.

The registry reports both a composite event count and a time-to-event estimate. That allows readers to distinguish a descriptive count from the sponsor’s primary inferential analysis. The confidence intervals also make uncertainty visible, rather than relying only on whether a p value appears small. Reading the effect measure, interval, endpoint definition, and analysis method together is essential to understanding what a result does and does not establish.

The posted secondary outcomes provide a further lesson: multiple endpoints may offer a broader view of trial outcomes, but they also raise questions about multiplicity and result selection. Without a reported testing hierarchy or adjustment plan, secondary p values need cautious interpretation. Likewise, missing details about analysis populations and missing-data handling limit how completely a reader can audit the evidence from the registry record.

Finally, the sample-size illustrations distinguish planning assumptions from observed trial evidence. They show how the required sample size changes when a smaller effect is targeted and how the power target affects planning, without implying that the trial’s own design used those assumptions. This separation helps prevent planning calculations from being mistaken for a measure of the trial’s observed success.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record leaves several details unavailable for independent assessment. The complete statistical analysis plan, original sample-size justification, interim analyses, and stopping rules are not reported. The planning illustrations use stated assumptions, but they do not establish the assumptions used in the original trial design.

For the primary composite, separate results for kidney failure, sustained eGFR decline, and renal death are not reported. The overall estimate therefore cannot show the contribution of each component. The record also does not report detailed subgroup estimates, making it impossible to evaluate variation in results across participant characteristics from these posted data.

The primary analysis population is named as the full analysis set, but its detailed definition is not reported. The methods for handling missing outcome information, loss to follow-up, and sensitivity analyses are also not reported. This limits assessment of how robust the estimates are to incomplete data or population-definition choices. The registry names a log-rank method but does not report the full model specification or all analysis details needed for an exact independent reproduction.

Some listed secondary outcomes have no posted results, and the multiplicity strategy is not reported. This makes it difficult to assess the inferential status of the posted secondary p values or the complete pattern across planned outcomes. Safety information is provided as counts and selected serious event terms, but does not include arm-specific figures for those terms or a detailed causal assessment.

These are limitations of what can be established from the registry record; they do not demonstrate that the trial investigators failed to conduct additional analyses or document additional procedures. The posted results should be interpreted within the information actually recorded for the study.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of Finerenone in Subjects With Type 2 Diabetes Mellitus and Diabetic Kidney Disease — NCT02540993.
• Registry record last updated 2023-07-24; status last verified 2023-07.
• Results first posted 2021-07-19.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT02540993 is a completed, randomized, double-blind, placebo-controlled, parallel-group, multicenter, event-driven Phase 3 study sponsored by Bayer. It enrolled 5734 participants with type 2 diabetes mellitus and diabetic kidney disease. Participants received finerenone 10 mg or 20 mg once daily, or matching placebo once daily, in addition to standard of care therapy.

The primary endpoint was time to first kidney failure, sustained eGFR decrease of at least 40% from baseline over at least 4 weeks, or renal death. The sponsor-reported log-rank analysis gave a hazard ratio of 0.825, 95% confidence interval from 0.732 to 0.928, and p = 0.001. The unadjusted recalculation from posted counts gave a risk difference of -0.033, with a 95% confidence interval from -0.054 to -0.013.

Some secondary outcomes and descriptive safety counts are posted. The original sample-size justification, full statistical analysis plan, multiplicity strategy, and detailed missing-data methods are not reported in the registry record.