Phase IIb Safety and Efficacy Study of Four Dose Regimens of BAY1021189 in Patients With Heart Failure and Preserved Ejection Fraction Suffering From Worsening Chronic Heart Failure (SOCRATES-PRESERVED): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase IIb Safety and Efficacy Study of Four Dose Regimens of BAY1021189 in Patients With Heart Failure and Preserved Ejection Fraction Suffering From Worsening Chronic Heart Failure (SOCRATES-PRESERVED) (NCT01951638), a randomized phase 2 study. The primary outcome is Change From Baseline to Week 12 in Log-transformed N-terminal Pro-brain Natriuretic Peptide (NT-proBNP).

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, placebo-controlled, double-blind, multicenter Phase II dose-finding trial. The registry describes the masking as quadruple. The study was intended to explore pharmacodynamic effects, safety and tolerability, and pharmacokinetics of four BAY1021189 dose regimens over 12 weeks in patients with worsening HFpEF. The stated objective was to identify an optimal once-daily oral dose for Phase III that could be used in addition to standard diuretic and comorbidity treatment.

The active regimens differed both in dose and titration. One group received 1.25 mg daily throughout treatment. Another received 2.5 mg daily throughout. A further regimen began at 2.5 mg daily and increased to 5 mg after 2 weeks, then continued at 5 mg. The highest titration regimen began at 2.5 mg daily, increased to 5 mg, and then increased to 10 mg. Placebo was given daily for 12 weeks. Sham titrations were described for the placebo and regimens without active dose changes.

The registry reports 477 enrolled participants. For the primary endpoint, the analysis population was the Per Protocol Set, defined as randomized participants with valid NT-proBNP measurements at baseline and Week 12 and no major protocol deviations. The reported arm counts for this endpoint were 73 for placebo, 77 for the 1.25 mg regimen, 78 for 2.5 mg, 57 for titration from 2.5 mg to 5 mg, and 60 for titration from 2.5 mg to 10 mg. These are endpoint-analysis counts, not a breakdown of all enrollment.

The trial status is completed. The registry record does not report the original sample-size justification or the trial’s original design assumptions. It also does not report further details of randomization implementation or concealment beyond the randomized allocation and masking labels.

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, 632 subjects were enrolled, of them 477 were randomized and 475 were treated. Among the 477 subjects who were randomized, 404 subjects completed both treatment and follow-up \[FU\] periods. All arms in FU period were mutually exclusive, this question below is ticked No because of database validation rule constraints.

Treatment Period

Reasons for not completing this period:

Follow-up Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per Protocol Set (PPS) NT-pro BNP: included all subjects randomized to treatment who had a valid measurement of NT-pro BNP at baseline and at Week 12 (Visit 5) and showed no major protocol deviations.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline to Week 12 in Log-transformed N-terminal Pro-brain Natriuretic Peptide (NT-proBNP), measured over Baseline, Week 12 (end of treatment [EOT]).

The primary endpoint was change from baseline to Week 12 in log-transformed N-terminal pro-brain natriuretic peptide (NT-proBNP), measured at the end of treatment. The registry describes NT-proBNP as a circulating plasma biomarker of cardiovascular function and prognosis in heart failure. The results are expressed as means with standard deviations on the log-transformed scale, rather than as raw NT-proBNP concentrations.

In general, a biomarker can provide a measurable biological outcome for a trial, while not necessarily capturing every aspect of how a patient feels or functions. A log transformation changes the scale on which values and differences are analyzed; a mean difference on that scale should therefore be read as a transformed-scale contrast, not as a raw-unit change in NT-proBNP. The registry record does not report a threshold for a clinically important change in this endpoint, so the posted mean differences cannot be labeled clinically important or unimportant on that basis.

The specified analysis population was the Per Protocol Set. It included randomized participants with valid NT-proBNP measurements at both baseline and Week 12 and no major protocol deviations. This definition makes clear that the primary endpoint summary does not represent every randomized participant. The registry record does not report further details about how missing endpoint measurements were handled.

7. Results Posted in the Registry

• BAY1021189 1.25 mg: mean -0.05 versus -0.10 on control; difference 0.05 (95% CI -0.20 to 0.30), standardized effect d = 0.07; z-test p = 0.690.
• BAY1021189 2.5 mg: mean 0.07 versus -0.10 on control; difference 0.17 (95% CI -0.09 to 0.42), standardized effect d = 0.21; z-test p = 0.193.
• BAY1021189 2.5 mg to 5 mg: mean 0.06 versus -0.10 on control; difference 0.15 (95% CI -0.12 to 0.43), standardized effect d = 0.19; z-test p = 0.274.
• BAY1021189 2.5 mg to 10 mg: mean -0.02 versus -0.10 on control; difference 0.08 (95% CI -0.18 to 0.33), standardized effect d = 0.10; z-test p = 0.560.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: each participant has a measured NT-proBNP value at baseline and Week 12, and the outcome is the change between those time points after log transformation. The registry reports the mean change and standard deviation for each treatment group. A mean describes the center of a group’s observed changes; a standard deviation describes how spread out those changes are around the group mean. A group mean is not the response of every participant, and the standard deviation is not a confidence interval for the mean.

What does the mean difference compare?

The recalculated comparisons subtract the placebo mean change from the corresponding active-regimen mean change on the transformed scale. For example, the reported recalculated difference for BAY1021189 1.25 mg is 0.051, and for 2.5 mg it is 0.169. Positive estimates indicate that the active group’s mean change is numerically higher than the placebo group’s mean change on this scale. This direction alone does not establish that the contrast is clinically favorable: the endpoint is transformed, and the registry record does not state a clinically important threshold or translate the differences into patient-level outcomes.

The recalculations use the posted group summaries to form simple, unadjusted contrasts. They are not adjusted analyses, and they do not substitute for the sponsor’s full analysis. The recalculated intervals and p-values describe the uncertainty under that simple comparison approach. The sponsor’s reported analyses are separately described as one-sided t-tests of log-scale mean differences.

How should a confidence interval be read?

In general, a confidence interval is a range generated by a statistical method to represent uncertainty around an estimate. It is not a range containing a fixed percentage of individual participants’ outcomes, and it does not mean that every value in the interval is equally likely. For each recalculated treatment-versus-placebo contrast, the interval spans zero. Zero represents no mean difference under the contrast definition. Thus the intervals do not exclude no difference, and they also include nonzero differences in either direction.

The interval’s width matters as well as whether it crosses zero. Wider intervals leave more uncertainty about the magnitude of a contrast. With group standard deviations around 0.7 to 0.8 on the transformed scale and the endpoint-analysis counts reported for each arm, uncertainty remains substantial relative to the estimated differences. This is a description of the posted summaries, not an explanation of why the trial had a particular design or outcome.

What does the p-value add?

In general, a p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor does it quantify the size or clinical importance of an effect. The recalculated p-values are unadjusted and correspond to the simple comparisons. They should be read alongside the effect estimates and confidence intervals, rather than as a standalone verdict.

The sponsor’s analyses use one-sided t-tests and report log-scale mean differences with confidence intervals. A one-sided test focuses on evidence in a specified direction, whereas a two-sided interval or test considers departures in either direction. The registry record does not report the detailed rationale for the one-sided specification. It is therefore important not to treat sponsor p-values and recalculated unadjusted p-values as if they came from identical methods.

Why do the analysis population and endpoint definition matter?

The primary endpoint population was the Per Protocol Set, not every person enrolled. The registry definition requires randomization, valid NT-proBNP measurements at baseline and Week 12, and no major protocol deviations. Restricting the summary to participants with those features can affect how well the comparison represents all randomized participants. The registry record does not report a separate intention-to-treat result or the number and reasons for missing endpoint measurements. It also does not report the methods used to address missing values.

In general, over-dispersion is a concern when the variability in observed outcomes is greater than a model assumes, because standard errors can then be too small and intervals too narrow. These posted continuous-outcome summaries use group standard deviations; the registry record does not describe a model for over-dispersion or a separate adjustment for it. No claim about such an adjustment can be made from the posted information.

What is and is not established by these methods?

The calculations describe between-group differences in average change in the specified biomarker over 12 weeks. They do not establish a causal pathway, a patient-level response pattern, a clinical benefit, or an optimal dose. The registry record does not report an analysis plan detailed enough to establish how all design choices, model assumptions, or testing procedures were specified in advance. The statistical interpretation should therefore stay with the defined endpoint, the stated population, the posted summaries, and the explicit uncertainty around the contrasts.

10. Confidence Intervals and Precision

The recalculated mean differences are modest relative to the uncertainty shown by their confidence intervals. The interval for each active regimen includes zero, so none of these recalculated intervals rules out no average difference from placebo. Each also allows differences in either direction. This is a statement about precision and compatibility with the data under the recalculation method, not proof that the regimens have identical effects.

In general, a confidence interval conveys both an estimate and its uncertainty. A narrow interval would constrain the plausible size of a contrast more closely, while a wide interval leaves greater uncertainty. Here, the recalculated intervals are wide enough to include zero and nonzero contrasts. The posted means and standard deviations likewise show that individual changes vary around their group means. Group-level summaries cannot reveal the full distribution or how many participants experienced changes in particular directions.

The sponsor reported confidence intervals for its log-scale mean differences. The registry lists a 90% interval for the placebo-only analysis and 95% intervals for the treatment comparisons. The sponsor’s intervals for the treatment comparisons also include zero. These reported intervals come with one-sided t-test analyses, whereas the recalculated intervals are simple unadjusted re-calculations. The two approaches should be distinguished rather than treated as interchangeable.

Precision is also limited by the analysis population definition. Only participants with valid measurements at baseline and Week 12 and no major protocol deviations were included in the primary endpoint set. The registry record does not report how missing endpoint data were addressed, so the effect of missingness on precision or representativeness cannot be assessed from the record.

11. 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 display is a planning illustration based on the observed treatment-versus-placebo effect, not the trial’s original design calculation. For these continuous-outcome comparisons, the reported figures are participants per arm, rather than total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The calculation considers detecting the stated fraction of the observed effect.

The 80% power column gives the planned number of participants per arm under those assumptions for a design with an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning number for a 90% chance under the same assumptions. Higher planned power generally requires more participants, all else equal. The figures are not an estimate of the probability that the completed trial found an effect.

The display includes scenarios for planning around 100%, 75%, and 50% of the observed effect. Smaller effects require more participants per arm to detect under the stated assumptions. The columns should be read as conditional planning scenarios, not as recommended trial sizes or evidence that any effect fraction is realistic. The original trial sample-size justification and its own design assumptions are not reported in the registry record. These figures are not observed power.

12. 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 = 0.051; pooled standard deviation σ = 0.783.
2. n = 2 × (1.96 + 0.842)² × 0.783² / 0.051² = 3,701.6, rounded up to 3,702 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 <- 0.051                      # observed difference in means
sigma <- 0.783151084798854                     # 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(1951638)
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 = 3,702 (80% power), 4,956 (90% power)
 75% of observed effect: n per arm = 6,581 (80% power), 8,810 (90% power)
 50% of observed effect: n per arm = 14,807 (80% power), 19,822 (90% power)
power.t.test: 3702.6 
Simulated power at n = 3,702 per arm: 0.797 (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.

13. Analyses Reported by the Sponsor

The registry reports sponsor analyses using one-sided t-tests of log-scale mean differences. For the treatment comparisons, the reported estimates are 0.052 for 1.25 mg, 0.171 for 2.5 mg, 0.156 for titration from 2.5 mg to 5 mg, and 0.076 for titration from 2.5 mg to 10 mg. The registry also reports 95% confidence intervals for those comparisons; each includes zero. The listed p-values are 0.657, 0.904, 0.865, and 0.719, respectively.

The recalculated unadjusted estimates are close to the sponsor’s reported estimates, but the methods are not identical. The recalculations use simple contrasts of posted group summaries, while the sponsor analyses are reported as one-sided t-tests. Their confidence intervals and p-values should therefore be interpreted according to their respective methods, not combined into a single test result. The registry record indicates no discrepancy between the posted results and the recalculations.

The sponsor also reports a placebo-only analysis with an estimate of 0.137, a 90% confidence interval from -0.04 to 0.31, and a listed p-value of 0.899. That is not a treatment-versus-placebo contrast, so it does not answer the primary comparative question by itself. The registry record does not explain the rationale for the placebo-only analysis or the one-sided testing specification.

14. Multiplicity, Missing Data and Analysis Populations

The primary endpoint compares four BAY1021189 regimens with a shared placebo group. The recalculated comparisons are unadjusted. The registry record does not report a multiplicity adjustment for the family of treatment comparisons, nor does it report a prespecified procedure for controlling the overall type I error across them. When multiple contrasts are considered, each unadjusted p-value does not by itself describe the strength of evidence across the full set of comparisons. The individual estimates and intervals remain useful descriptions, but they should not be treated as a single confirmatory test of all regimens.

The registry lists five outcome measures and ten analyses, but no secondary outcomes are posted in the outcome results. The registry record does not report whether there were interim analyses or how any interim testing was handled. It also does not report the full statistical analysis plan, including whether the primary contrast or dose-selection approach was specified in advance.

The primary endpoint was analyzed in the Per Protocol Set. This set required a valid NT-proBNP measurement at baseline and Week 12 and no major protocol deviations. The registry record does not report an intention-to-treat analysis of the primary endpoint, the number or reasons for missing measurements, or the method used to handle missing data. It is therefore not possible to assess from the record whether missingness could have affected the estimates or how sensitive the results are to alternative assumptions.

The registry record does not report the original sample-size justification or the assumptions used to plan enrollment. The planning figures associated with the posted comparisons are illustrations based on observed effects, not evidence of the trial’s original design rationale. These gaps do not negate the reported summaries, but they limit assessment of how the trial’s testing strategy, analysis population, and precision were planned.

15. 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: cardiac failure (7.4%), acute kidney injury (4.2%), cardiac failure chronic (4.2%), cardiac failure acute (3.2%), cardiac failure congestive (3.2%).

The registry reports serious adverse events by treatment group, including the number at risk, the number affected by a serious adverse event, other adverse events, and deaths. For serious adverse events, the recorded affected counts were 20 in the placebo group, 20 with BAY1021189 1.25 mg, 24 with 2.5 mg, 18 with titration from 2.5 mg to 5 mg, and 21 with titration from 2.5 mg to 10 mg. The corresponding at-risk counts were 93, 96, 95, 95, and 96.

Deaths were recorded as 1 for placebo, 0 for 1.25 mg, 1 for 2.5 mg, 7 for titration from 2.5 mg to 5 mg, and 2 for titration from 2.5 mg to 10 mg. These are descriptive counts. The registry record does not establish that a treatment caused an event, and raw counts alone do not account for timing, duration of exposure, or participant characteristics.

The registry lists serious-event terms including cardiac failure at 7.4%, acute kidney injury at 4.2%, cardiac failure chronic at 4.2%, cardiac failure acute at 3.2%, cardiac failure congestive at 3.2%, and pneumonia at 3.1%. The record does not provide enough detail in these summaries to interpret those term percentages as treatment-specific comparisons. Safety counts should be read as part of the reported trial record, not as a stand-alone assessment of risk.

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

The posted results describe mean change in log-transformed NT-proBNP from baseline to Week 12 among participants in the Per Protocol Set. Group means ranged from -0.098 for placebo to 0.071 for BAY1021189 2.5 mg. The recalculated treatment-versus-placebo mean differences were 0.051, 0.169, 0.155, and 0.075 across the four active regimens. Their confidence intervals all include zero, so the registry summaries do not show a precisely determined average difference from placebo for any regimen under the simple recalculation.

This does not establish that the regimens and placebo are equivalent, nor does it establish that an effect is absent. The intervals allow uncertainty in both direction and magnitude. The sponsor’s reported treatment comparisons likewise have intervals including zero, but use one-sided t-tests and should be considered separately from the simple recalculations.

The endpoint is a transformed biomarker measure, not a direct outcome such as symptoms, hospital admission, or survival. The registry record identifies NT-proBNP as a biomarker of cardiovascular function and prognosis in heart failure, but does not provide a threshold for interpreting a given difference as clinically important. The results therefore cannot by themselves establish a clinical benefit or identify a best dose.

The study’s stated aim was dose selection for Phase III, with BAY1021189 added to standard diuretic and comorbidity treatment. The posted endpoint results are relevant to that dose-finding objective, but the record does not provide a reported selection rule or a clinical-outcome comparison that would settle dose choice. Safety information is also descriptive and does not support a causal conclusion from the counts alone. Interpretation should remain limited to the reported biomarker summaries, analysis population, uncertainty, and safety records.

17. Why This Trial Matters Statistically

This trial illustrates why dose-finding results need to be read through both the endpoint definition and the analysis population. The primary outcome is a transformed biomarker measured at baseline and Week 12, while the analysis excludes randomized participants without valid measurements at both times or with major protocol deviations. Those choices define what the reported means represent and limit direct generalization to all enrolled participants.

It also shows why an estimated difference should not be detached from its uncertainty. All recalculated confidence intervals include zero, and the estimates are not precise enough to rule out no mean difference. At the same time, that uncertainty is not proof that the groups are identical. A plain statement of the point estimates alone would miss this important distinction.

The multiple dose regimens create several comparisons against a shared placebo group. Unadjusted estimates can be informative for describing each contrast, but multiplicity and the absence of a reported detailed analysis plan complicate any claim based on selecting the most favorable-looking comparison. The registry record does not report the original sample-size justification, so the planning illustrations should not be confused with the trial’s design rationale.

Finally, the endpoint is a biomarker and the stated purpose was selection of a dose for further study. The statistical question answered by these results is narrower than whether treatment changes patients’ clinical experience or outcomes. Keeping that distinction clear is central to responsible interpretation of early-phase clinical evidence.

18. 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 results apply to the Per Protocol Set, whose definition requires valid measurements at baseline and Week 12 and no major protocol deviations. They do not represent every enrolled participant. The registry record does not report an intention-to-treat result, the number and reasons for missing endpoint measurements, or the missing-data method, so the potential impact of exclusions cannot be assessed from the record.

The outcome is log-transformed NT-proBNP. The registry describes the biomarker’s relevance to cardiovascular function and prognosis but does not report a threshold for clinically important change or a translation of the transformed-scale contrasts into raw concentrations. The posted result therefore has limits as a measure of patient-centered benefit.

The recalculated comparisons are unadjusted, and the registry record does not report a multiplicity adjustment for the four treatment comparisons. Sponsor results use one-sided t-tests, while recalculations are simple contrasts from posted summaries. The registry does not report the rationale for one-sided testing or enough detail to establish that the approaches share the same assumptions.

The original sample-size justification, original design assumptions, interim-analysis plan, and full statistical analysis plan are not reported in the registry record. Planning illustrations based on observed effects cannot fill those gaps. The safety summaries are counts and listed event terms; the registry record does not establish causality or provide enough information in these summaries to make detailed treatment-specific safety comparisons.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Phase IIb Safety and Efficacy Study of Four Dose Regimens of BAY1021189 in Patients With Heart Failure and Preserved Ejection Fraction Suffering From Worsening Chronic Heart Failure (SOCRATES-PRESERVED) — NCT01951638.
• Registry record last updated 2021-03-16; status last verified 2021-02.
• Results first posted 2021-02-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed randomized, parallel-group, placebo-controlled, double-blind Phase II trial of BAY1021189 in patients with worsening HFpEF. The primary endpoint was change from baseline to Week 12 in log-transformed NT-proBNP, analyzed in the Per Protocol Set. Four dose regimens were compared with placebo.

The posted and recalculated treatment comparisons have confidence intervals that include zero. The recalculated contrasts are unadjusted, and the sponsor’s reported analyses use one-sided t-tests. The record also reports serious adverse events and deaths by group. The findings are limited to the biomarker endpoint, defined analysis population, and descriptive safety information; the registry record does not report the original sample-size justification or a detailed account of missing-data handling.