A Study to Test the Effect of Different Doses of BI 685509 on Kidney Function in People With Diabetic Kidney Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Test the Effect of Different Doses of BI 685509 on Kidney Function in People With Diabetic Kidney Disease (NCT04750577), a randomized phase 2 study. The primary outcome is Change From Baseline in Log Transformed Urine Albumin Creatinine Ratio (UACR) Measured in 10-hour Urine After 20 Weeks of Trial Treatment.

2. Clinical Question

3. Trial Design

This completed phase 2 study used randomized allocation and a parallel-group design, with placebo as the comparator. The registry describes the trial as quadruple masked and the official title specifies double-blinding within dose groups. It tested three BI 685509 dose regimens against placebo. The registry record lists 243 enrolled participants.

Treatment lasted 20 weeks for the primary endpoint. Participants took tablets three times a day and continued their usual treatment for diabetes and kidney disease. For the 2 mg regimen, the description notes titration from a low dose to a medium dose. For the 3 mg regimen, it notes titration from low to medium and then high dose. The 1 mg regimen is listed without a titration description.

The primary outcome was analyzed using UACR measurements collected at baseline and follow-up visits. The reported longitudinal analysis incorporated measurements from baseline (Week -2 and Week -1) and Week 6, Week 12, and Week 20, with the reported least-squares means referring to Week 20. The registry describes the analysis population as the Full Analysis Set, defined by baseline and post-baseline measurement requirements.

The listed secondary outcomes examined UACR measured in first-morning-void urine and the number of participants meeting a threshold for UACR decrease in 10-hour or first-morning-void urine. Trial start was 2021-04-27, primary completion was 2022-11-30, and the registry status is completed. The original sample-size justification and other design assumptions 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: All subjects were screened for eligibility prior to participation in the trial. Subjects attended a specialist site which ensured that they (the subjects) strictly met all inclusion and none of the exclusion criteria. Subjects were not to be allocated to a treatment group if any of the entry criteria were violated.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS): The patient set included all patients who had at least one baseline measurement of UACR in week -2, -1, or 0 and at least one post-baseline measurement after week 6.

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: Randomised Set (RS): This patient set includes all entered and randomised patients.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Log Transformed Urine Albumin Creatinine Ratio (UACR) Measured in 10-hour Urine After 20 Weeks of Trial Treatment, measured over The MMRM model is a longitudinal analysis and it incorporated UACR measurements from baseline (Week -2 and Week -1) and Week 6, Week 12 and Week 20. The data represent the Least Squares Mean at Week 20..

The primary endpoint was change from baseline in log-transformed urine albumin-to-creatinine ratio (UACR), measured in 10-hour urine after 20 weeks of treatment. UACR expresses urine albumin relative to urine creatinine. The registry describes the 10-hour collection as starting after the first-morning-void sample: subsequent urine passed during the collection period was collected, and an aliquot was used for the 10-hour UACR measurement.

Log transformation is commonly used for measurements whose values are skewed or whose variability increases with their magnitude. In general, working on a logarithmic scale can make statistical modeling more suitable and makes the estimated change a change on that transformed scale, rather than a direct difference in mg/g. The outcome is therefore not interpreted as a raw change in UACR concentration.

UACR was used to assess a kidney-related biological measure over the treatment period. It can provide information about albumin excretion, but it is not itself a measure of long-term kidney failure, symptoms, or survival. The primary analysis used a repeated-measures model and reported a least-squares mean at Week 20. The model incorporated measurements from multiple visits, rather than relying only on a single observed measurement at the end of treatment.

The Full Analysis Set included participants with a qualifying baseline UACR measurement and at least one post-baseline measurement after week 6. Details of how missing measurements were handled beyond the stated model and population definition are not reported in the registry record.

7. Results Posted in the Registry

• BI 685509 1 mg TID: mean -0.07 versus 0.03 on control; difference -0.10 (95% CI -0.31 to 0.10), standardized effect d = -0.19; z-test p = 0.322.
• BI 685509 2mg TID: mean -0.03 versus 0.03 on control; difference -0.06 (95% CI -0.27 to 0.15), standardized effect d = -0.11; z-test p = 0.558.
• BI 685509 3 mg TID: mean -0.22 versus 0.03 on control; difference -0.25 (95% CI -0.46 to -0.04), standardized effect d = -0.45; z-test p = 0.017.

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.

Change From Baseline in Log Transformed Urine Albumin Creatinine Ratio (UACR) Measured in First Morning Void Urine After 20 Weeks of Trial Treatment

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • BI 685509 1 mg TID: mean -0.11 versus 0.10 on control; difference -0.21 (95% CI -0.41 to -0.01), standardized effect d = -0.39; z-test p = 0.038.
  • BI 685509 2mg TID: mean -0.02 versus 0.10 on control; difference -0.12 (95% CI -0.32 to 0.09), standardized effect d = -0.22; z-test p = 0.256.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for BI 685509 1 mg TID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BI 685509 2mg TID and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients Achieving UACR Decreases in 10-hour Urine of at Least 20% From Baseline After 20 Weeks of Trial Treatment

• 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:
  • BI 685509 1 mg TID: 40.4% (23/57) versus 23.2% (13/56) on control; risk difference 17.1 percentage points (95% CI 0.3 to 34.0), risk ratio 1.74 (0.98–3.08); unadjusted two-proportion z-test p = 0.051.
  • BI 685509 2mg TID: 30.2% (16/53) versus 23.2% (13/56) on control; risk difference 7.0 percentage points (95% CI -9.6 to 23.6), risk ratio 1.30 (0.69–2.44); unadjusted two-proportion z-test p = 0.410.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BI 685509 1 mg TID and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BI 685509 2mg TID and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients Achieving UACR Decreases in First Morning Void Urine of at Least 20% From Baseline After 20 Weeks of Trial Treatment

• 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:
  • BI 685509 1 mg TID: 40.4% (23/57) versus 19.6% (11/56) on control; risk difference 20.7 percentage points (95% CI 4.3 to 37.2), risk ratio 2.05 (1.11–3.81); unadjusted two-proportion z-test p = 0.016.
  • BI 685509 2mg TID: 24.5% (13/53) versus 19.6% (11/56) on control; risk difference 4.9 percentage points (95% CI -10.7 to 20.5), risk ratio 1.25 (0.61–2.54); unadjusted two-proportion z-test p = 0.538.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for BI 685509 1 mg TID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BI 685509 2mg TID and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary UACR assessment in two ways: they examine first-morning-void UACR as a continuous measure and count participants who met a threshold for UACR decrease in either 10-hour or first-morning-void urine. Together, these outcomes give a view of whether the pattern seen for the primary 10-hour measure is also apparent using a different urine collection or a threshold-based definition.

Across the listed outcomes, findings are not uniform across all dose groups or all ways of measuring UACR. The broad pattern offers some correspondence with the primary result, but it is not a consistent demonstration that every dose or measurement method produces the same estimated response. The secondary results therefore provide context rather than replacing the primary endpoint. Their measures are related to UACR, but differ in collection method, scale, or definition of response.

Unadjusted secondary results carry less weight because several outcomes and treatment comparisons are examined. In general, the more hypotheses tested, the greater the chance that at least one result may appear noteworthy by chance if multiplicity is not handled. The registry record lists the secondary analyses and their reported results but does not report a complete multiplicity strategy. The threshold outcomes also reduce a continuous measurement to whether a participant crossed a cutoff, which discards information about the size of change.

These secondary outcomes should be interpreted as supportive and exploratory in relation to the primary result. They do not establish a clinical outcome beyond the UACR measures, and their uncertainty should be considered alongside the sponsor’s primary repeated-measures analysis. No additional conclusion about long-term kidney outcomes is reported in the registry record.

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

• Change From Baseline in Log Transformed Urine Albumin Creatinine Ratio (UACR) Measured in First Morning Void Urine After 20 Weeks of Trial Treatment
• Number of Patients Achieving UACR Decreases in 10-hour Urine of at Least 20% From Baseline After 20 Weeks of Trial Treatment
• Number of Patients Achieving UACR Decreases in First Morning Void Urine of at Least 20% From Baseline After 20 Weeks of Trial Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint was analyzed with a restricted maximum likelihood-based mixed-effect model for repeated measures (REML-based MMRM). In general, a repeated-measures model uses observations from multiple visits while accounting for the fact that measurements from the same participant are related. That approach can make use of the longitudinal pattern rather than treating every measurement as independent. The registry says that measurements from baseline, Week 6, Week 12, and Week 20 were incorporated, and that the least-squares mean at Week 20 was reported.

What does the repeated-measures model estimate?

The model estimates an adjusted mean change for each treatment group and a difference between each dose group and placebo. A least-squares mean is a model-based estimate, not simply the arithmetic average of the observed values. The sponsor’s analysis included fixed categorical effects of treatment at each visit, a continuous baseline effect at the follow-up visits, and random effects of patient. In general, adjustment and repeated-measures modeling can account for the planned structure of the measurements, but the model’s estimates still depend on its specification and on assumptions about the data.

The primary outcome was log-transformed UACR. The reported treatment differences therefore refer to the transformed outcome. In general, a log scale can be useful when measurements are right-skewed or when variability changes with the measurement level. It also means the estimate should not be read as a direct difference in raw mg/g. Interpretation on the original scale would require an appropriate transformation, and no such additional result is needed to describe the posted model estimates.

Why are there multiple dose-response models?

The registry reports MCP-Mod fits using exponential, linear, quadratic, Emax, and sigmoid Emax models. MCP-Mod is a general approach for assessing dose-response patterns by considering candidate shapes rather than assuming that response changes in only one specific way. A linear shape assumes a straight-line trend across doses; other shapes can represent curvature or a response that levels off. The model-fit p-values reported for the primary endpoint differ across these candidate forms. The record does not report a single preferred shape or enough detail to reconstruct all model assumptions.

In general, testing several dose-response shapes raises a multiplicity question: results may look more compelling when multiple candidate tests are considered unless the analysis plan accounts for that process. The registry lists the model-fit p-values but does not report the multiplicity adjustment or decision rule in enough detail to determine how the set of tests was interpreted.

What do the recalculated comparisons represent?

The additional comparisons are simple unadjusted recalculations from posted arm summaries. For a continuous outcome, such a comparison contrasts the arm means using a pooled estimate of variability. It is not the same as the sponsor’s repeated-measures analysis, which uses longitudinal measurements and model-based adjustment. The recalculated confidence intervals and p-values can therefore differ from the registry’s own estimates. Since a discrepancy is flagged, the sponsor’s own analysis takes precedence.

In general, unadjusted comparisons can be useful as a transparent check on the direction and rough scale of a result, but they may not preserve the original trial’s modeling choices or analysis population. The registry’s reported model is the more relevant source for interpreting the primary endpoint as analyzed by the sponsor.

Why does over-dispersion matter for some outcomes?

Over-dispersion is a general issue for count or binary data when observed variability is greater than a model expects. If it is ignored, standard errors and confidence intervals may be too optimistic. The posted primary outcome is continuous and analyzed with an MMRM, so over-dispersion is not the central issue for that endpoint. The secondary threshold outcomes are binary counts and use logistic regression in the registry analyses; the record does not report an over-dispersion adjustment for those analyses.

For binary outcomes, logistic regression estimates an odds ratio, which compares the odds of meeting the outcome between groups. An odds ratio is not the same as a risk difference or a ratio of probabilities. The registry’s threshold outcomes are secondary and the posted results should be read with their uncertainty and multiplicity context in mind.

11. Confidence Intervals and Precision

A confidence interval describes a range of estimates compatible with the data and the statistical model at the stated confidence level. It is not a guarantee that the true effect lies inside the interval, and it does not describe the range of individual participant outcomes. In general, a narrower interval indicates greater precision, while a wider interval indicates more uncertainty about the effect’s size.

For the sponsor’s primary repeated-measures comparisons, the 1 mg estimate was -0.103 with a 95% confidence interval from -0.309 to 0.102. The interval includes zero, so the result is compatible with both a more negative difference and a small positive difference under that model. The 2 mg estimate was -0.063, with a 95% confidence interval from -0.275 to 0.150; this interval also includes zero. The 3 mg estimate was -0.251, with a 95% confidence interval from -0.459 to -0.043, which lies on the negative side of zero.

These intervals reflect uncertainty in the mean differences on the log-transformed UACR scale. They do not capture every source of uncertainty, such as uncertainty about the model form, the choice among dose-response shapes, missing-data assumptions, or whether the trial’s result would be reproduced in another study. The registry record does not report all information needed to assess those sources fully.

The sponsor’s intervals differ slightly from the simple recalculated intervals because the analyses are not identical. The sponsor’s longitudinal model is the primary reported analysis and takes precedence over the unadjusted recalculations. Precision should therefore be judged from the sponsor’s model-based estimates and their confidence intervals, while keeping the short treatment period and biomarker nature of the outcome 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 sample-size entries are planning illustrations based on the observed effect, not the trial’s original design justification. For these continuous and binary outcomes, the entries mean participants per arm, not a total across arms or a total number of events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The trial’s own original design assumptions are not reported in the registry record.

The 80% power column describes the planned number of participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the other assumptions were correct. The 90% power column describes the corresponding planning target for a 90% chance. These are design probabilities, not guarantees about a future study’s result.

Rows for planning for 75% or 50% of the observed effect assume a smaller effect than the observed one. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under otherwise similar assumptions. The curve communicates the same general dependence between the effect size assumed for planning and the sample size required.

These values are not observed power. They are not a retrospective measure of whether the completed trial was adequately powered, and they do not change the uncertainty in the observed estimates. They are illustrations that depend on the observed effect, which itself is uncertain.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.103; pooled standard deviation σ = 0.553.
2. n = 2 × (1.96 + 0.842)² × 0.553² / -0.103² = 451.8, rounded up to 452 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.103                      # observed difference in means
sigma <- 0.552575558406041                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(4750577)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 452 (80% power), 605 (90% power)
 75% of observed effect: n per arm = 804 (80% power), 1,076 (90% power)
 50% of observed effect: n per arm = 1,808 (80% power), 2,420 (90% power)
power.t.test: 452.8 
Simulated power at n = 452 per arm: 0.796 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses using repeated-measures models for the primary endpoint and MCP-Mod fits for dose-response. The sponsor’s primary comparisons are model-based and use measurements across visits. For those comparisons, the registry reports mean differences, confidence intervals, and p-values for each dose relative to placebo. The dose-response model fits are reported separately, with candidate shapes and their corresponding p-values.

The additional recalculations use posted arm-level summaries to make simple, unadjusted comparisons. They do not reproduce the sponsor’s longitudinal model, its use of repeated observations, or necessarily its exact analysis population. Accordingly, small differences between the recalculated and sponsor estimates, confidence limits, or p-values should not be treated as evidence that either set of numbers is an exact duplicate of the other.

A discrepancy is flagged for this trial. Under that circumstance, the sponsor’s own analysis takes precedence. For primary-outcome interpretation, the sponsor’s reported repeated-measures estimates and confidence intervals are therefore the relevant results; the recalculations are secondary checks, not replacements. The registry record does not explain the discrepancy in detail, so its source is not reported in the registry record.

The distinction also matters for the secondary outcomes. The sponsor reported logistic regression analyses for threshold outcomes, whereas simple recalculations can express comparisons on other scales. Those approaches answer related but not identical statistical questions. The sponsor’s reported analysis should be used when describing the trial’s own findings, with the limitations of the registry’s reporting kept in view.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several statistical hypotheses are tested. In this trial, the record reports comparisons of three dose groups with placebo, multiple MCP-Mod dose-response shapes for the primary endpoint, and several secondary endpoints. If each test is interpreted without accounting for the overall set, the chance of at least one apparently positive result can increase. General approaches to multiplicity include prespecifying a testing sequence, adjusting significance thresholds, or treating some analyses as exploratory.

The registry record lists p-values for five MCP-Mod model fits and sponsor comparisons for the dose groups. It does not report enough detail about the prespecified testing hierarchy, adjustment method, or decision rule to determine how multiplicity across these tests was handled. The record also does not report a complete strategy for the secondary analyses. Consequently, isolated p-values should not be read as if they were necessarily adjusted confirmatory findings.

The primary analysis population is described as the Full Analysis Set. It included participants with at least one qualifying baseline UACR measurement in week -2, -1, or 0 and at least one post-baseline measurement after week 6. The primary model incorporated measurements from baseline, Week 6, Week 12, and Week 20. This definition clarifies who could contribute to the analysis, but it is not a complete account of how all randomized participants were handled.

Missing-data methods beyond the stated model and population definition are not reported in the registry record. In general, repeated-measures models can use available observations, but interpretation depends on assumptions about why measurements are missing and how missingness relates to observed or unobserved outcomes. The registry record does not give enough information to assess those assumptions, any sensitivity analyses, or the handling of withdrawals and other incomplete outcome data. Interim analyses and sample-size justification are also not reported in the registry record.

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: acute myocardial infarction (1.7%), nodal rhythm (1.7%), epiploic appendagitis (1.7%), hypoglycaemia (1.7%), angina unstable (1.6%).

The registry lists serious adverse events for each treatment group alongside the number at risk for that group. The reported serious adverse event counts were 4 among 61 at risk in the 1 mg group, 8 among 61 at risk in the 2 mg group, 7 among 61 at risk in the 3 mg group, and 4 among 58 at risk in the placebo group. These are descriptive counts; no causal conclusion about treatment can be drawn from the counts alone.

The registry also lists deaths as 0, 1, 2, and 0 in the 1 mg, 2 mg, 3 mg, and placebo groups, respectively. The record does not establish from these figures whether any event or death was caused by study treatment. Serious events listed among the leading terms include acute myocardial infarction, nodal rhythm, epiploic appendagitis, hypoglycaemia, unstable angina, and atrial fibrillation. The registry gives 1.7% for several listed terms and 1.6% for others.

Adverse-event counts are not measures of comparative risk on their own. They should be considered with the group denominators, the duration of follow-up, event definitions, and the registry’s completeness. The safety figures do not establish long-term safety or explain the clinical circumstances of individual events.

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

The results describe changes in UACR during a 20-week treatment period in a randomized, placebo-controlled trial. UACR is a kidney-related urine measure, and the primary outcome was its change on a logarithmic scale. The sponsor’s analysis reports different estimated comparisons across the dose groups; the 3 mg comparison’s confidence interval is on the negative side of zero, while the intervals for the 1 mg and 2 mg comparisons include zero.

That statistical pattern is not the same as demonstrating a change in long-term kidney function or a benefit that participants would notice. The primary endpoint is a biomarker, and the registry record does not report a primary outcome based on kidney failure, symptoms, or survival. The result also does not establish what the effect would be after longer treatment or in people outside the trial’s described population.

A confidence interval gives an indication of uncertainty around the estimated group difference under the analysis model. It does not establish that an effect is clinically important, nor does a p-value measure the probability that the treatment effect is real. The reported estimates are compatible with a range of possible magnitudes, and the record does not supply a threshold for what would count as a clinically important UACR change.

The findings also need to be read with the analysis details in mind. The sponsor used a longitudinal model and multiple dose-response models, while the additional recalculations are unadjusted. A discrepancy is flagged, so the sponsor’s own analysis takes precedence. Multiplicity handling and missing-data details are not reported in the registry record. These limitations constrain how firmly the observed pattern can be generalized or interpreted.

In short, the registry reports a dose-specific pattern in a measured urine outcome over the trial period. It does not by itself establish clinical benefit, long-term kidney outcomes, or a definitive dose-response relationship.

18. Why This Trial Matters Statistically

This trial illustrates why a reported treatment effect needs to be read together with its outcome definition, analysis model, and precision. The primary outcome was not a single raw UACR observation: it was change in log-transformed UACR, estimated at Week 20 using measurements collected across visits. The model-based estimate and its confidence interval answer a different question from a simple comparison of group averages.

The study also demonstrates how a dose-ranging trial can use multiple candidate dose-response shapes. The MCP-Mod results vary across the exponential, linear, quadratic, Emax, and sigmoid Emax fits. That variation makes the assumed shape and multiplicity strategy relevant to interpretation; a single p-value cannot summarize all the evidence about dose response.

Secondary endpoints use related but distinct definitions, including first-morning-void urine and threshold-based decreases. Agreement across measures can add context, while inconsistency can signal that the result depends on the measurement or analysis choice. In this record, the pattern is not identical across all endpoints and dose groups, so the primary analysis remains central.

Finally, the record shows the value of distinguishing sponsor analyses from simple recalculations. The sponsor’s repeated-measures model reflects the stated longitudinal analysis, whereas unadjusted re-calculations from posted summary statistics are checks rather than substitutes. The flagged discrepancy makes that distinction especially important. Clear reporting of multiplicity, missing-data handling, and original design assumptions would further support independent assessment, but those details are not reported in the registry record.

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 primary endpoint is a biomarker measured over 20 weeks, so it does not directly establish long-term kidney outcomes. The record describes UACR changes but does not report a primary clinical endpoint based on kidney failure, symptoms, or survival. Any interpretation should remain specific to the measured outcome and follow-up period.

The registry record does not report the trial’s original sample-size justification or the design assumptions used to choose enrollment. The planning illustrations based on observed effects do not fill that gap. Nor does the record provide enough detail to assess the multiplicity strategy across dose comparisons, candidate dose-response models, and secondary outcomes.

The Full Analysis Set definition requires baseline and post-baseline UACR measurements, but additional missing-data handling details and sensitivity analyses are not reported in the registry record. The record also does not explain the flagged discrepancy between the recalculated results and the sponsor’s analyses. The sponsor’s own analysis takes precedence, but the reason for the discrepancy is not reported in the registry record.

The secondary outcomes use different urine collection approaches and threshold definitions, which limits direct comparability with the primary endpoint. The registry’s safety counts are descriptive and do not establish causation. Finally, the study is phase 2 and the primary follow-up is 20 weeks; the record alone cannot establish persistence of the observed pattern beyond that period or its applicability beyond the studied population.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Test the Effect of Different Doses of BI 685509 on Kidney Function in People With Diabetic Kidney Disease — NCT04750577.
• Registry record last updated 2024-07-23; status last verified 2024-07.
• Results first posted 2024-07-23.
• 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

NCT04750577 is a completed phase 2 randomized, quadruple-masked, parallel-group, placebo-controlled trial sponsored by Boehringer Ingelheim. It enrolled 243 participants and tested BI 685509 at 1 mg, 2 mg, and 3 mg against matching placebo in adults with diabetic kidney disease. Trial start was 2021-04-27, and primary completion was 2022-11-30.

The primary endpoint was change from baseline in log-transformed UACR measured in 10-hour urine after 20 weeks. The sponsor reported repeated-measures comparisons and MCP-Mod dose-response fits. Three secondary UACR outcomes were posted, alongside adverse-event counts. The sponsor’s analysis takes precedence over the unadjusted recalculations because a discrepancy is flagged. Multiplicity handling, further missing-data details, and the trial’s original sample-size assumptions are not reported in the registry record.