A Trial to Study Neladenoson Bialanate Over 20 Weeks in Patients With Chronic Heart Failure With Reduced Ejection Fraction: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Trial to Study Neladenoson Bialanate Over 20 Weeks in Patients With Chronic Heart Failure With Reduced Ejection Fraction (NCT02992288), a randomized phase 2 study. The primary outcome is Absolute Change From Baseline in Left Ventricular Ejection Fraction (LVEF) (%) at Week 20 Measured by Echocardiography.

2. Clinical Question

The question is about change in a cardiac measurement over the trial period, not about whether participants experienced fewer hospitalizations or deaths. Those outcomes appear among the secondary measures, but corresponding arm-level results are not reported in the registry record. The reported primary endpoint summaries are means and standard deviations. They describe average changes and the spread of individual changes within each group; they do not by themselves establish a dose-response relationship or a clinical effect.

3. Trial Design

This was a Phase II, randomized, placebo-controlled, parallel-group, multicenter trial of neladenoson bialanate in people with HFrEF. The registry lists enrollment of 427. Participants were assigned to one of five dose groups—5 mg, 10 mg, 20 mg, 30 mg, or 40 mg—or placebo. Treatment was studied over 20 weeks, and the stated objective was to find an optimal once-daily oral dose when used in addition to standard therapy for HFrEF.

The record describes the trial as double blind and quadruple masked. It does not identify which people or study roles were masked, nor does it report the allocation ratio or the detailed randomization procedure. The trial status is completed. The recorded study start was 2017-02-22 and the primary completion date was 2018-03-28.

The primary outcome was absolute change from baseline in LVEF at Week 20, measured by echocardiography. Its arm-level results are for a per-protocol set, not the full enrollment population. The registry describes that set as participants without validity findings affecting efficacy evaluation, but the available definition is cut off; complete rules for eligibility in this analysis are not reported in the registry record.

Other registered outcomes include changes in left ventricular end-systolic volume, left ventricular end-diastolic volume, and high-sensitivity troponin T, as well as composite efficacy and cardiovascular or heart-failure event outcomes. The registry records 8 outcome measures and 25 analyses. Detailed design assumptions, the trial’s original sample-size justification, and the complete statistical analysis plan 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: Overall, 462 participants were screened. Of them, 35 participants did not complete screening due to unmet eligibility criteria, consent withdrawal, adverse events and other unspecified reasons. In total, 427 participants were randomized and 426 participants received study treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per-protocol set (PPS) included all participants without validity findings affecting efficacy evaluation. The participants with invalid/missing baseline or missing post-baseline LVEF values not due to cardiovascular (CV) death or heart failure (HF) hospitalization or with other major protocol deviation were excluded from PPS LVEF 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) included all randomized participants.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Absolute Change From Baseline in Left Ventricular Ejection Fraction (LVEF) (%) at Week 20 Measured by Echocardiography, measured over Baseline, Week 20.

The primary endpoint is absolute change from baseline in left ventricular ejection fraction (LVEF), expressed as a percentage of LVEF and measured by echocardiography at Week 20. LVEF is a measure of how much blood the left ventricle ejects with each contraction. A change score compares the Week 20 measurement with the baseline measurement for each participant; the posted group summaries report the mean of these changes and their standard deviations.

As a continuous endpoint, LVEF change can retain information about the magnitude of change rather than reducing each participant’s result to a yes-or-no event. General statistical context: continuous outcomes can be useful in trials when the question concerns whether a measure shifts on average between groups. The standard deviation describes how variable the individual changes were around each group mean, while a confidence interval for a group contrast expresses uncertainty about the estimated difference in means.

The registry identifies the endpoint as the primary measure of efficacy and uses echocardiography for its assessment. It does not report a threshold defining a clinically important change, nor does it explain the clinical interpretation assigned to a particular magnitude of LVEF change. The endpoint therefore supports a comparison of the recorded changes, but should not be treated alone as a complete measure of participants’ symptoms, function, hospitalization, or survival.

7. Results Posted in the Registry

• Neladenoson Bialanate 5 mg: mean 2.59 versus -2.19 on control; difference 4.78 (95% CI 0.28 to 9.28), standardized effect d = 0.57; z-test p = 0.038.
• Neladenoson Bialanate 10 mg: mean -3.01 versus -2.19 on control; difference -0.82 (95% CI -5.03 to 3.39), standardized effect d = -0.09; z-test p = 0.702.
• Neladenoson Bialanate 20 mg: mean 0.13 versus -2.19 on control; difference 2.32 (95% CI -1.14 to 5.78), standardized effect d = 0.27; z-test p = 0.189.
• Neladenoson Bialanate 30 mg: mean -2.45 versus -2.19 on control; difference -0.26 (95% CI -4.31 to 3.79), standardized effect d = -0.03; z-test p = 0.900.

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 Left Ventricular End-Systolic Volume (LVESV) at Week 20

• 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 deviations.
• Result:
  • Neladenoson Bialanate 5 mg: mean -21.41 versus -5.44 on control; difference -15.97 (95% CI -39.61 to 7.67), standardized effect d = -0.42; z-test p = 0.186.
  • Neladenoson Bialanate 10 mg: mean -2.82 versus -5.44 on control; difference 2.62 (95% CI -12.41 to 17.65), standardized effect d = 0.08; z-test p = 0.733.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Neladenoson Bialanate 5 mg 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 Neladenoson Bialanate 10 mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Left Ventricular End-Diastolic Volume (LVEDV) at Week 20

• 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 deviations.
• Result:
  • Neladenoson Bialanate 5 mg: mean -21.65 versus -13.16 on control; difference -8.49 (95% CI -38.63 to 21.65), standardized effect d = -0.18; z-test p = 0.581.
  • Neladenoson Bialanate 10 mg: mean -12.44 versus -13.16 on control; difference 0.72 (95% CI -16.79 to 18.23), standardized effect d = 0.02; z-test p = 0.936.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Neladenoson Bialanate 5 mg 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 Neladenoson Bialanate 10 mg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in High Sensitivity Troponin T (Hs-TNT) at Week 20

• 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 deviations.
• Result:
  • Neladenoson Bialanate 5 mg: mean 6.46 versus 0.13 on control; difference 6.33 (95% CI -5.89 to 18.55), standardized effect d = 0.34; z-test p = 0.310.
  • Neladenoson Bialanate 10 mg: mean 3.77 versus 0.13 on control; difference 3.64 (95% CI -2.50 to 9.78), standardized effect d = 0.22; z-test p = 0.245.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Neladenoson Bialanate 5 mg 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 Neladenoson Bialanate 10 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary measures broaden the assessment beyond LVEF. They include changes in left ventricular end-systolic volume, left ventricular end-diastolic volume, and high-sensitivity troponin T, alongside composite efficacy, cardiovascular mortality, and heart-failure hospitalization or urgent-visit outcomes. These outcomes are related to heart failure but are not interchangeable with the primary echocardiographic measure.

The posted continuous summaries show variation between groups, with substantial spread in several measures. The sponsor-reported MCP-Mod analyses for the posted secondary continuous measures do not show a statistically significant dose-response result at the conventional 0.05 threshold. The record does not report numerical arm-level results for all the registered secondary outcomes, so no overall conclusion about the composite or event outcomes can be drawn from the available results.

The secondary results do not overturn or independently confirm the primary result. They provide additional context about cardiac volumes and a biomarker, while the primary endpoint measures LVEF change. If several secondary outcomes and contrasts are examined, isolated unadjusted findings carry less weight because multiple testing increases the possibility of chance findings. The registry record does not report the multiplicity strategy for the secondary endpoints or identify a hierarchy assigning confirmatory status to each one.

Accordingly, secondary measures are best treated as supportive or exploratory unless the trial’s analysis plan specifies otherwise. The complete plan is not reported in the registry record. Their results can help describe the pattern of measurements, but cannot establish a treatment effect on outcomes whose numerical results are absent or replace the sponsor’s primary dose-response analysis.

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

• Change From Baseline in Left Ventricular End-Systolic Volume (LVESV) at Week 20
• Change From Baseline in Left Ventricular End-Diastolic Volume (LVEDV) at Week 20
• Change From Baseline in High Sensitivity Troponin T (Hs-TNT) at Week 20
• Number of Participants With Composite Efficacy Outcome
• Number of Participants With Cardiovascular (CV) Mortality
• Number of Participants With Heart Failure (HF) Hospitalization and Urgent Visits for Heart Failure (HF)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference represent?

The primary outcome is continuous, so the posted group summaries describe mean change in LVEF and standard deviation. A mean difference compares the average change in one dose group with the average change in the placebo group. A positive difference means the estimated mean change was numerically higher in the dose group; it does not by itself establish that the difference is reliable, important to patients, or caused by treatment.

The recalculated comparisons are unadjusted, simple comparisons based on the posted summary statistics. General statistical explanation: an unadjusted comparison evaluates one contrast without accounting for the fact that many contrasts or outcomes may have been examined. When multiple tests are considered, the chance of at least one apparently unusual result can rise. The sponsor’s analysis is therefore important, particularly because the trial’s stated aim was dose finding rather than simply identifying one favorable dose-specific contrast.

What does the confidence interval say?

A confidence interval describes uncertainty around an estimated group difference under the assumptions of the analysis. It gives a range of values compatible with the observed data and method; it is not a range containing a known proportion of individual participant outcomes. For a mean difference, an interval that includes zero is compatible with no mean difference as well as with differences in either direction. An interval that excludes zero is evidence against a zero difference under that particular comparison, but does not resolve multiplicity or establish clinical importance.

The recalculated intervals are based on the arm means, standard deviations, and analysis counts recorded for the endpoint. They are not the sponsor’s full dose-response analysis. The record does not provide sponsor confidence intervals for the reported MCP-Mod tests.

Why is the sponsor’s dose-response analysis relevant?

The registry reports MCP-Mod analyses across placebo and all five dose groups. General statistical explanation: MCP-Mod is a framework used in dose-finding studies to evaluate dose-response patterns using candidate response shapes while accounting for the range of doses studied. This differs from treating each dose as an isolated pairwise comparison with placebo. The registry does not describe the candidate response models or all implementation details, so the reported analysis cannot be reconstructed from the record alone.

Because the record flags a discrepancy between the reported analysis and the unadjusted recalculations, the sponsor’s own analysis takes precedence. The unadjusted comparisons remain useful as descriptive, simple contrasts, but they should not replace the sponsor’s dose-response result.

What does the standard deviation contribute?

The standard deviation describes the dispersion of participant-level changes around the group mean. General statistical explanation: a larger standard deviation indicates more variability in individual measurements. Variability affects the precision of a mean and the ability of a study to distinguish a group contrast from random variation. It is not the same thing as the standard error or a confidence interval; those also depend on the number of observations used in the analysis.

The observed endpoint counts differ by group, and the endpoint is reported for the per-protocol set. General statistical explanation: unequal group sizes can lead to different precision across arm summaries, even when the outcome’s variability is similar. The registry record does not give a complete account of exclusions or missing-data handling for this endpoint, so the reported counts should be interpreted as analysis counts rather than assumed to represent every randomized participant.

What do the p-values mean?

A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the model’s assumptions. It is not the probability that the null hypothesis is true, nor a direct measure of effect size. The unadjusted p-value for 5 mg is below 0.05, but that single result must be considered alongside the multiple dose comparisons and the sponsor’s MCP-Mod analysis. The sponsor’s reported dose-response p-values are not below 0.05.

Statistical significance does not establish clinical importance, and a result above a threshold does not prove that groups are equivalent. Confidence intervals and the size and direction of the estimates help describe what the data are compatible with. The registry does not report a prespecified clinically important LVEF difference, so the clinical meaning of the estimated differences cannot be settled from the posted endpoint summaries alone.

11. Confidence Intervals and Precision

The recalculated mean differences have varying precision. The 5 mg versus placebo interval excludes zero, while the intervals for the other dose comparisons include zero. For those other comparisons, the posted estimates are compatible with a range that includes no mean difference as well as values on either side. This uncertainty matters: an estimated difference is not a precise account of the true group contrast.

Interval width reflects both the spread of participant outcomes and the number of observations contributing to a comparison. The analysis counts vary by dose, and the standard deviations are substantial in relation to the mean changes. General statistical explanation: when observations are highly variable or the analysis group is small, a mean difference is generally estimated less precisely. This is one reason that the apparent size of a point estimate should not be read without its interval.

The 5 mg comparison has an unadjusted interval that does not include zero, but this does not remove uncertainty about the dose-response question. It is one of several unadjusted comparisons, and the sponsor’s own MCP-Mod analysis takes precedence because the record flags a discrepancy. The sponsor’s reported dose-response result does not meet the conventional 0.05 threshold. The record does not provide confidence intervals for that sponsor analysis.

Confidence intervals are not guarantees that a future study will reproduce the same estimate. They also do not address potential bias from missing observations, analysis-population selection, or multiplicity unless those issues are incorporated into the method. The complete missing-data approach and the full analysis plan are not reported in the registry record. The arm-level summaries should therefore be read with the stated per-protocol population and the limits of the posted analysis in mind.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations estimate participants per arm for two-sided comparisons under the stated assumptions: significance level 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is expressed as a fraction of the observed effect. These are planning illustrations based on the observed result, not the trial’s original design assumptions, which are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the stated effect under those assumptions, if that effect and model assumptions hold. The 90% power column gives the corresponding estimate for a 90% chance. These are design targets, not guarantees. Each figure is per arm; the sample-size method is not a total-events method.

The rows for 100%, 75%, and 50% of the observed effect illustrate how the planning estimate changes when the effect to detect is smaller than the observed estimate. Smaller effects need more participants to detect with the same target power, all else equal. This is especially important when the observed estimate is uncertain: planning from a single trial’s observed effect can produce an optimistic or unstable illustration.

This is not observed power. It does not describe the probability that the completed trial detected an effect after its results were known. The trial’s own sample-size rationale and original planning assumptions are not reported in the registry record, so the illustrations should not be mistaken for the design basis of this study.

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 = 4.780; pooled standard deviation σ = 8.415.
2. n = 2 × (1.96 + 0.842)² × 8.415² / 4.780² = 48.7, rounded up to 49 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 <- 4.78                      # observed difference in means
sigma <- 8.41540978651664                     # 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(2992288)
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 = 49 (80% power), 66 (90% power)
 75% of observed effect: n per arm = 87 (80% power), 116 (90% power)
 50% of observed effect: n per arm = 195 (80% power), 261 (90% power)
power.t.test: 49.6 
Simulated power at n = 49 per arm: 0.790 (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 the sponsor’s primary dose-response analyses using MCP-Mod across placebo and the five dose groups. It also permits simple recalculations of dose-versus-placebo mean differences from the posted arm means and standard deviations. Those recalculations are unadjusted pairwise comparisons; they are not substitutes for the sponsor’s dose-response method.

A discrepancy is flagged between the recalculated results and the sponsor’s reported analysis. In that situation, the sponsor’s own analysis takes precedence. The sponsor’s reported MCP-Mod p-values are all above the conventional 0.05 threshold. The registry does not provide enough methodological detail to reconstruct every part of that analysis or to determine the specific source of the discrepancy.

The unadjusted 5 mg comparison has a p-value of 0.038 and an interval excluding zero. That nominal result should not be presented as the trial’s overall primary conclusion: it is one of several dose comparisons, while the stated objective was dose finding and the sponsor’s analysis assessed dose-response across the groups. The other simple recalculations do not show similarly small unadjusted p-values. Together, the two analyses answer related but distinct questions, and the sponsor’s reported analysis is the appropriate basis for interpreting the trial’s primary dose-response result.

15. Multiplicity, Missing Data and Analysis Populations

There are several dose groups and multiple registered outcomes. The primary sponsor analysis uses MCP-Mod across the groups, while the posted recalculations also include several unadjusted dose-versus-placebo comparisons. General statistical explanation: when multiple hypotheses are tested, the chance of at least one small p-value can increase if each test is interpreted separately without an appropriate strategy. Thus the unadjusted p-value for one dose should not be treated as if it were the only test planned.

The registry reports five MCP-Mod p-values for the primary endpoint and further reported MCP-Mod results for the continuous secondary measures. It does not explain the relationship among each reported p-value and candidate model, give the full testing hierarchy, or describe a multiplicity adjustment for all primary and secondary analyses. Those details are not reported in the registry record. The sponsor’s reported primary analysis takes precedence over simple recalculations because a discrepancy is flagged.

The primary endpoint population is described as the per-protocol set. The registry says it included participants without validity findings affecting efficacy evaluation, but the remaining definition is truncated. The full criteria for the per-protocol analysis population are therefore not reported in the registry record. The analysis counts differ across endpoints and groups, but the record does not give a complete explanation of exclusions or missing observations.

The registry identifies some exclusions involving invalid or missing baseline or post-baseline LVEF values, and refers to exceptions related to cardiovascular death or heart-failure hospitalization, but the available population description is incomplete. The imputation approach, sensitivity analyses for missing data, and handling of intercurrent events are not reported in the registry record. The original sample-size justification, interim analyses, and complete statistical plan are also not reported. These omissions limit independent assessment of how the analyses were selected and how robust the results are to alternative assumptions.

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: cardiac failure (18.9%), cardiac failure chronic (4.7%), atrial fibrillation (4.2%), renal impairment (4.2%), anaemia (2.9%).

The registry records participants at risk and participants affected by serious adverse events for each group. For placebo, 31 participants were affected among 106 at risk. The corresponding figures are 13 among 37 for 5 mg, 28 among 70 for 10 mg, 22 among 72 for 20 mg, 28 among 69 for 30 mg, and 26 among 72 for 40 mg. These are participant counts, not counts of all serious-event episodes.

For other adverse events, the registry records 24 participants affected among 106 at risk for placebo; 10 among 37 for 5 mg; 15 among 70 for 10 mg; 18 among 72 for 20 mg; 24 among 69 for 30 mg; and 19 among 72 for 40 mg. Recorded deaths were 8 for placebo, 1 for 5 mg, 5 for 10 mg, 1 for 20 mg, 2 for 30 mg, and 2 for 40 mg. The registry record does not provide the context needed to interpret each death or establish its relationship to study treatment.

The listed serious-event terms include cardiac failure, chronic cardiac failure, atrial fibrillation, renal impairment, anaemia, and atrial flutter, with percentages recorded for each term. These figures describe reported events; they do not establish causality or comparative risk. The registry does not report a detailed safety analysis plan in the information summarized for these results.

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

The results describe mean changes in LVEF over 20 weeks among participants included in the per-protocol analysis. The estimates vary across placebo and the five dose groups, and individual changes show substantial variability. The sponsor’s reported MCP-Mod analyses do not establish a statistically significant dose-response pattern at the conventional 0.05 threshold. The recalculated 5 mg comparison is nominally different from placebo, but it is an unadjusted result among several contrasts and does not take precedence over the sponsor’s analysis.

This statistical reading does not establish that neladenoson bialanate does or does not improve health outcomes. LVEF is one measured cardiac outcome, and the available primary result does not by itself answer questions about symptoms, quality of life, hospitalization, or survival. Although several such outcomes are registered as secondary measures, complete numerical results for them are not reported in the registry record.

The trial was a Phase II dose-finding study with follow-up over 20 weeks. Results from this design and period should not be extended to outcomes or follow-up durations that are not represented in the posted results. The registry does not report a clinically important threshold for LVEF change, so statistical differences should not be equated with clinically meaningful differences.

Uncertainty also remains about the analysis population, missing-data handling, multiplicity strategy, and full statistical plan. These are relevant when judging how much weight to place on an isolated comparison or on the overall pattern. The posted results support a description of the measured changes and sponsor analysis, but do not settle broader questions about efficacy, safety, or the best dose.

18. Why This Trial Matters Statistically

This trial illustrates why a dose-finding question is not the same as a collection of separate pairwise comparisons. With several doses, one unadjusted comparison can appear more persuasive than the overall dose-response analysis. Here, the simple 5 mg recalculation is nominally different from placebo, while the sponsor’s reported MCP-Mod analyses do not establish a dose-response result at the conventional threshold. The distinction is important for avoiding selective interpretation of a single contrast.

It also demonstrates the value of looking beyond point estimates. The mean changes differ across groups, but the standard deviations indicate considerable variability, and several recalculated intervals include zero. A numerical difference alone does not show how precisely the effect is estimated. Confidence intervals and the analysis method help readers distinguish observed direction from strength of evidence.

The trial’s registered secondary measures span cardiac structure, a biomarker, and clinical events. Such measures can complement the primary endpoint, but they require an explicit interpretation strategy, especially when many outcomes are considered. The registry record does not report the complete multiplicity plan or all secondary outcome results, leaving limits on how much can be inferred across the full outcome set.

Finally, the sample-size illustrations show how planning depends on the effect size one aims to detect, while the trial’s original sample-size rationale is not reported. This distinction helps prevent retrospective planning calculations from being mistaken for evidence that the completed study was adequately powered for every outcome or dose comparison.

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 results are reported for a per-protocol set, and the available description of that population is truncated. This limits assessment of who was included and excluded from the primary analysis. Although the registry mentions invalid or missing LVEF measurements, the full handling of missing data and the reasons for differing analysis counts are not reported in the registry record.

The sponsor’s analysis is reported as MCP-Mod, but its model specifications and full implementation details are not included. A discrepancy is flagged between the reported analysis and simple unadjusted recalculations; the sponsor’s analysis takes precedence, but the source of the discrepancy cannot be assessed from the registry record. The registry also does not report the complete multiplicity strategy or the full statistical analysis plan.

The results concern a 20-week endpoint in a Phase II dose-finding trial. The primary measure is echocardiographic LVEF change, and the record does not identify a clinically important threshold for interpreting the size of that change. Several registered secondary clinical outcomes lack numerical results in the posted information, limiting assessment of broader clinical outcomes.

Safety counts are descriptive. The registry results listed do not provide enough detail to establish whether individual events or deaths were caused by treatment, or to assess the full context of each event. The original sample-size justification, interim analyses, and further protocol details are not reported in the registry record. These limitations constrain interpretation but do not change the reported group summaries or sponsor analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Trial to Study Neladenoson Bialanate Over 20 Weeks in Patients With Chronic Heart Failure With Reduced Ejection Fraction — NCT02992288.
• Registry record last updated 2019-04-23; status last verified 2019-04.
• Results first posted 2019-04-23.
• 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

NCT02992288 is a completed, randomized, placebo-controlled, parallel-group Phase II trial of once-daily oral neladenoson bialanate added to standard therapy for HFrEF. It enrolled 427 participants and studied five doses over 20 weeks. The primary endpoint was change from baseline in echocardiographic LVEF at Week 20, reported for a per-protocol set.

The recalculated unadjusted 5 mg comparison differs from placebo, but the sponsor’s own MCP-Mod analysis takes precedence because a discrepancy is flagged. The sponsor’s reported primary dose-response analyses do not meet the conventional 0.05 threshold. Secondary measures and safety outcomes add descriptive context, although complete numerical results and analysis details are not reported for all registered outcomes.

The record does not provide the complete statistical plan, original sample-size rationale, or full missing-data and multiplicity procedures. The posted findings should therefore be interpreted as trial-specific estimates for the stated outcomes and analysis population, not as conclusions about outcomes beyond those recorded.