Effect of Serelaxin Versus Standard of Care in Acute Heart Failure (AHF) Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Serelaxin Versus Standard of Care in Acute Heart Failure (AHF) Patients (NCT02064868), a randomized phase 3 study. The primary outcome is Percentage of Participants With Worsening Heart Failure (WHF) / All Cause of Deaths Through Day 5.

2. Clinical Question

The primary endpoint combines worsening heart failure and all-cause death within the stated follow-up period. The worsening-heart-failure definition focused on worsening signs or symptoms that led to intensification of intravenous heart-failure therapy or to mechanical ventilation, renal support, or circulatory support. A central event adjudication committee oversaw adjudication of the worsening-heart-failure endpoint.

The comparison is between a treatment strategy that added serelaxin to usual background management and a strategy of standard care alone. It therefore addresses the added treatment in the context of standard care, rather than serelaxin in isolation. The registry record does not report additional eligibility details or explain the rationale for the chosen endpoint beyond its definition.

3. Trial Design

This was a randomized, parallel-group, open-label Phase 3 study of serelaxin plus standard of care versus standard of care alone in participants hospitalized for acute heart failure. The registry record describes the study as prospective, multinational, and multicenter. It records enrollment of 2666 participants and status as terminated. The recorded study start was 2014-01-31, and primary completion was 2017-03-26. The reason for termination is not reported in the registry record.

The serelaxin group received a continuous 48-hour intravenous infusion at 30 µg/kg/day alongside standard of care. Participants in both groups were required to receive background heart-failure management according to local guidelines or international standards. The record notes that standard care could include intravenous and/or oral diuretics, among other treatments. It does not provide a complete account of each participant’s background treatment.

Masking was listed as none, so the study was open-label. The registry record does not report details of how the randomization sequence was generated or concealed, or whether outcome assessors other than the central event adjudication committee were masked. It also does not report the trial’s original sample-size justification, planned interim analyses, or full statistical analysis plan.

The primary outcome was assessed through Day 5 in the Full Analysis Set. Listed secondary outcomes include heart-failure events or readmission through Day 14, persistent signs or symptoms or non-improvement through Day 5, renal deterioration through Day 14, index hospital stay length, adverse events, and change in health-related quality of life measured with the EuroQoL EQ-5D-5L questionnaire. The registry record lists these outcome topics but does not report full numerical results for every listed outcome.

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: The initial target was to randomize 3183 patients. This study was prematurely terminated (due to the neutral read-out of study RELAX-AHF-2) after 2666 patients were randomized. 16 patients had not qualified for randomization but were inadvertently randomized. These 16 patients did not enter the treatment phase and were not counted as started.

Overall Study

Reasons for not completing this period:

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

5. Baseline Characteristics

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

Population: Full Analysis Set

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Worsening Heart Failure (WHF) / All Cause of Deaths Through Day 5, measured over 5 days.

The primary endpoint was the percentage of participants with worsening heart failure or all-cause death through Day 5. For worsening heart failure, the registry definition required worsening signs or symptoms that led to an escalation of care: intensification of intravenous heart-failure therapy, mechanical ventilation, or renal or circulatory support. A central event adjudication committee was appointed to oversee adjudication of the worsening-heart-failure endpoint. The endpoint’s stated population was the Full Analysis Set.

A composite endpoint combines more than one type of event into a single outcome. This can capture several clinically relevant ways in which a participant’s condition may worsen, but the components are not necessarily interchangeable in importance or frequency. The percentage for the composite does not by itself show how many events came from each component. The registry record does not report separate primary-endpoint counts for worsening heart failure and all-cause death.

Using a defined follow-up window makes the comparison specific to events occurring through Day 5; it does not describe outcomes beyond that window. The primary outcome is binary at the participant level for the posted percentage: a participant either met the event definition during the stated period or did not. The registry record does not provide further detail about how events after discharge, if any, were handled for this endpoint.

7. Results Posted in the Registry

• Standard of Care (SOC): 6.9% (62/894) versus 5.0% (87/1756) on control; risk difference 2.0 percentage points (95% CI 0.0 to 3.9), risk ratio 1.40 (1.02–1.92); unadjusted two-proportion z-test p = 0.036.

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.

Percentage of Participants With In-hospital Worsening Heart Failure/All-Cause Death/Readmission for Heart Failure Through Day 14

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Standard of Care (SOC): 10.6% (95/894) versus 8.5% (149/1756) on control; risk difference 2.1 percentage points (95% CI -0.3 to 4.5), risk ratio 1.25 (0.98–1.60); unadjusted two-proportion z-test p = 0.071.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Standard of Care (SOC) and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Persistent Sign or Symptoms of Heart Failure / Non-Improvement at Any Post Baseline Visit Through Day 5

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Standard of Care (SOC): 91.1% (814/894) versus 86.0% (1500/1744) on control; risk difference 5.0 percentage points (95% CI 2.6 to 7.5), risk ratio 1.06 (1.03–1.09); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Standard of Care (SOC) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Renal Deterioration at Any Post Baseline Visit Through Day 14

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Standard of Care (SOC): 44.0% (391/889) versus 36.0% (626/1740) on control; risk difference 8.0 percentage points (95% CI 4.0 to 12.0), risk ratio 1.22 (1.11–1.35); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Standard of Care (SOC) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes address several aspects of the hospital course and follow-up: additional heart-failure events or readmission, persistence of signs or symptoms, renal deterioration, length of the index hospital stay, adverse events, and health-related quality of life. The detailed posted comparisons cover heart-failure events through Day 14, persistent signs or symptoms through Day 5, and renal deterioration through Day 14. Other listed secondary outcome topics do not have detailed numerical results reported in the registry record.

Across the detailed secondary comparisons, the event percentages are lower in the serelaxin-plus-standard-of-care group than in the standard-of-care group. The registry’s reported tests are more supportive for the symptom and renal outcomes than for the Day 14 heart-failure composite. This broad pattern offers context alongside the primary outcome, but it does not change what the primary endpoint measured or extend its follow-up window.

Secondary outcomes differ in definition, timing, and clinical meaning. For example, a persistent symptom outcome is not interchangeable with a composite of heart-failure events, death, or readmission, and neither is equivalent to a renal outcome. Their patterns can be informative when considered together, but should not be collapsed into one overall treatment effect.

General statistical explanation: testing multiple secondary outcomes creates more opportunities for a nominally notable result to occur by chance. The registry record does not report a multiplicity adjustment or a hierarchy for secondary testing. Therefore, unadjusted secondary findings carry less weight than a prespecified primary result and are best treated as supporting or hypothesis-generating evidence. They should not be presented as independent confirmations without accounting for the number of comparisons and the analysis plan.

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

• Percentage of Participants With In-hospital Worsening Heart Failure/All-Cause Death/Readmission for Heart Failure Through Day 14
• Percentage of Participants With Persistent Sign or Symptoms of Heart Failure / Non-Improvement at Any Post Baseline Visit Through Day 5
• Percentage of Participants With Renal Deterioration at Any Post Baseline Visit Through Day 14
• Length of Index Hospital Stay
• Percentage of Participants With Adverse Events as Assessment of Safety and Tolerability of Serelaxin in AHF Patients
• Change From Baseline in Health-related Quality of Life Index Value, Assessed by EuroQoL EQ-5D-5L Questionnaire.

9. Statistical Interpretation

10. Statistical Methods Explained

The main statistical summaries describe event proportions, differences between proportions, and the registry’s own reported analysis. Each answers a related but distinct question. The outcome is a percentage of participants with an event, while the sponsor-reported analysis gives a hazard ratio and a test result. The methods below explain these ideas generally and distinguish the posted calculations from the trial’s reported analysis.

What does a risk difference describe?

A risk difference subtracts one group’s event probability from the other group’s event probability. Its scale is an absolute difference in probability, rather than a relative comparison. The direction depends on which group is subtracted from which. For the primary recalculation, the contrast is standard of care minus serelaxin plus standard of care, so a positive estimate corresponds to a higher observed event percentage in the standard-of-care group. The risk difference can be read alongside the group percentages to understand the absolute scale of the contrast.

A risk difference does not, on its own, adjust for other variables or account for event timing. The posted recalculation is described as a simple unadjusted recalculation from the summary statistics. It should therefore be understood as a descriptive, unadjusted comparison rather than as a reconstruction of every detail of the sponsor’s statistical model.

How is a confidence interval used?

In general, a confidence interval expresses the range of estimates reasonably compatible with the observed data under the method’s assumptions. Its width conveys precision: narrower intervals indicate more precise estimates, while wider intervals indicate greater uncertainty. For a risk difference, zero is the value corresponding to no difference on that scale. For a ratio such as a hazard ratio, one is the value corresponding to no relative difference. These reference values help readers interpret whether an interval includes the null value, but an interval is not a probability statement about the true effect.

What does the p-value say?

In general, a p-value measures how compatible the observed data are with a specified null hypothesis under the test’s assumptions. It is not the probability that the null hypothesis is true, and it does not indicate the magnitude or practical importance of a difference. A smaller p-value can reflect stronger incompatibility with the null model, but interpretation also depends on the analysis plan, data quality, and whether multiple outcomes or analyses were considered.

The primary recalculation reports an unadjusted p-value, while the registry separately reports the result of its own test. The two values arise from different summaries and methods. They should not be combined or presented as if they were replicate estimates from one identical analysis. The registry record does not report a full analysis plan explaining how the primary testing procedure was chosen or whether other planned analyses were conducted.

What is the registry-reported analysis?

The registry names Gehan’s generalized Wilcoxon test and reports a hazard ratio. In general, a hazard ratio compares event rates over time between groups, subject to the assumptions and setup of the model used. A ratio below one indicates a lower estimated hazard in the numerator group relative to the denominator group, if that is how the comparison is parameterized. The record identifies the group order and labels the test as superiority, but does not give enough information to independently reconstruct the analysis, including all model details or handling of censoring.

The generalized Wilcoxon family of tests gives weight to the timing of events in comparing groups. The exact interpretation of the posted hazard ratio depends on the sponsor’s analysis specification. The registry record does not report those details beyond the named method, the hazard-ratio estimate, its interval, and the p-value. For that reason, the reported analysis should be quoted as recorded rather than treated as a result that can be recreated from the event percentages alone.

Why can the methods yield different numerical results?

General statistical explanation: a comparison of the proportions with an event by a fixed time summarizes whether an event occurred within that window. A hazard-based analysis uses information about when events occurred and may also incorporate censoring. Because these summaries use different information and estimands, their estimates and p-values need not match exactly. Differences between them do not automatically mean one calculation is erroneous.

For the primary endpoint, the posted arm percentages and the recalculated risk difference are straightforward summaries of the event proportions. The sponsor-reported analysis is a separate result using the named test and hazard-ratio summary. The record does not supply the participant-level event times or full analysis specification needed to reproduce that sponsor result independently.

How should secondary tests be read?

Secondary endpoints can provide context about other outcomes, but they are not the same question as the primary endpoint. General statistical explanation: when many outcomes or tests are examined, the chance of at least one apparently notable result can increase. A multiplicity procedure can control or otherwise address that issue, depending on its design. The registry record does not report whether a multiplicity adjustment was planned or applied. Consequently, unadjusted secondary p-values should be treated as exploratory or supportive evidence rather than as equivalent in evidential status to a prespecified primary analysis.

Different endpoint types also call for different summaries. Binary outcomes are expressed as event percentages, whereas length of stay and a change in a quality-of-life index would require other summaries. The registry lists those outcome topics, but detailed values and statistical methods for all of them are not reported in the registry record. The method attached to one outcome should not be assumed to have been used for every other outcome.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty remains around an estimate. For the primary recalculated risk difference, the 95% confidence interval extends from < 0.001 to 0.039. Because the interval is close to zero at its lower bound, the data are consistent with a small positive difference on the stated scale as well as with larger positive differences within the interval. The interval does not include zero, but that fact does not establish the clinical importance of the estimate.

The sponsor-reported hazard ratio is 0.71, with a 95% confidence interval from 0.51 to 0.98. This interval is for a ratio, so the null reference is one rather than zero. The interval does not include one, but the hazard ratio and risk difference are different measures. Their interval widths cannot be directly compared as if they shared a common scale.

In general, a confidence interval reflects sampling uncertainty under the method used; it does not capture every source of uncertainty. It does not resolve possible issues related to missing data, outcome ascertainment, analysis choices, or generalizability. The registry record does not report enough detail to assess all those sources for this trial.

For secondary endpoints, the posted intervals vary by outcome and should be read on each outcome’s own scale. An interval that includes the no-difference value indicates that the data are compatible with no difference under that calculation, as well as with values on either side allowed by the interval. An interval excluding that value does not by itself account for multiple testing or establish clinical relevance. Precision and evidential strength are therefore related but distinct considerations.

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 illustrations are planning calculations based on the observed effect, not on the trial’s original design assumptions. For these binary outcomes, the entries are participants per arm. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s original sample-size justification and assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the calculation estimates would be needed for an 80% chance of detecting the specified effect under the stated assumptions. The 90% power column gives the corresponding planning target for a 90% chance. These are design-planning quantities: they relate to the chance of a statistically significant result if the assumed effect and model were true, not to certainty that a study will find an effect.

Rows for smaller fractions of the observed effect require more participants per arm, because a smaller difference is harder to distinguish from random variation. The illustrations are sensitive to the assumed event rates and effect size, so they should not be read as a retrospective judgment that the trial was adequately or inadequately designed. They are not observed power.

The calculations are not a substitute for the original protocol’s sample-size rationale. The registry record does not report whether the trial’s initial design used the same assumptions, whether its planned effect differed, or whether any design changes were made. The illustrations are best read as conditional planning examples using the stated assumptions and the effect estimates in the posted results.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.050; treatment proportion p₁ = 0.069; average p̄ = 0.059.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3344 = 0.6554.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3341 = 0.2812.
4. n = (0.6554 + 0.2812)² / (0.0198)² = 2,236.1, rounded up to 2,237 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.0495444191343964                          # control proportion
p1 <- 0.0693512304250559                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2064868)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 2,237 (80% power), 2,994 (90% power)
 75% of observed effect: n per arm = 3,821 (80% power), 5,115 (90% power)
 50% of observed effect: n per arm = 8,246 (80% power), 11,039 (90% power)
power.prop.test: 2236.1 
Simulated power at n = 2,237 per arm: 0.798 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry-reported primary analysis used Gehan’s generalized Wilcoxon test and gave a hazard ratio of 0.71, a 95% confidence interval from 0.51 to 0.98, and p = 0.017. It is labeled as a superiority analysis. Separately, a simple unadjusted recalculation from the posted event summaries gives a risk difference of 0.020, a 95% confidence interval from < 0.001 to 0.039, and an unadjusted p-value of 0.036.

These results do not express the comparison in the same way. The risk difference summarizes the contrast in event proportions, whereas the registry-reported hazard ratio and named test reflect the sponsor’s reported analysis. A difference in numerical values or p-values is therefore not, by itself, evidence of a contradiction. The registry record does not provide enough detail to reproduce the sponsor’s full analysis from the summary statistics.

The registry record does not flag a discrepancy between the reported analysis and the recalculation. The sponsor’s reported analysis should be presented as the trial’s own analysis, while the recalculation is useful as a transparent, unadjusted summary of the posted event proportions. Neither should be described as a replacement for the other.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is identified, and the registry gives its analysis method and result. However, the registry record does not report a complete statistical analysis plan or state whether the primary analysis was adjusted for any interim monitoring or other planned comparisons. Interim analyses are not reported in the registry record. Their absence from the record should not be interpreted as proof that none occurred.

The registry lists several secondary outcomes, and detailed results include multiple comparisons. A multiplicity strategy—such as a prespecified hierarchy or adjustment to the testing threshold—is not reported in the registry record. Without that information, the secondary p-values should be interpreted as unadjusted unless the registry explicitly says otherwise. This affects how confidently nominal evidence across several endpoints can be interpreted.

The primary outcome population is stated as the Full Analysis Set. The registry record does not define the membership rules for that set or explain whether it corresponds to all randomized participants under an intention-to-treat approach. It also does not report how missing primary-outcome data were handled, how participants with incomplete follow-up were classified, or whether sensitivity analyses assessed alternative missing-data assumptions.

For secondary outcomes, the analyzed participant counts vary across outcome records. The registry record does not explain all reasons for these differences or specify a common missing-data method across endpoints. In general, missing-data handling can influence an estimate when the chance of missingness is related to outcome status or group assignment. No such relationship should be assumed from the counts alone.

The study was open-label, so treatment assignment was not masked. The central event adjudication committee is reported for the worsening-heart-failure endpoint, which is a methodological safeguard for event classification. The record does not give further details about adjudication procedures, masking of assessors, or how other outcomes were ascertained. These omissions limit independent assessment of outcome measurement and analysis choices.

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 1.5% 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 (2.9%), pneumonia (0.7%), renal impairment (0.6%), acute kidney injury (0.5%), acute myocardial infarction (0.4%).

The posted safety figures give serious adverse events for each group alongside the number at risk: 214 participants among 1729 at risk in the serelaxin-plus-standard-of-care group, and 107 among 894 at risk in the standard-of-care group. The record also gives other adverse-event counts and deaths: 637 other events among 1729 at risk and 63 deaths in the serelaxin group, and 324 other events among 894 at risk and 43 deaths in the standard-of-care group. These are counts with their recorded denominators; they are not causal estimates.

The listed serious adverse-event terms include cardiac failure at 2.9%, pneumonia at 0.7%, renal impairment at 0.6%, acute kidney injury at 0.5%, acute myocardial infarction at 0.4%, and unstable angina at 0.4%. The registry record does not specify in this listing whether each term’s percentage is pooled or group-specific, so the terms should not be read as an arm-by-arm comparison.

Safety counts describe events recorded during the study and do not, by themselves, establish whether an event was caused by the assigned treatment. The open-label design and absence of fuller detail on event collection and attribution limit further interpretation. The record does not provide a complete narrative safety analysis in the information summarized for these outcomes.

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

The posted primary results show a lower observed percentage for the composite of worsening heart failure or all-cause death through Day 5 in the serelaxin-plus-standard-of-care group than in the standard-of-care group. The unadjusted risk-difference interval is close to zero at its lower end, while the registry-reported analysis also reports a hazard ratio with an interval that does not include one. These are the results of the posted analyses, expressed using different statistical summaries.

That finding does not establish the size of any effect with certainty. Confidence intervals describe statistical precision under their assumptions, and the recalculated interval allows a range of possible differences. The p-values do not quantify clinical importance or the probability that the finding is true. The composite outcome also does not show which component contributed the events, because separate primary component results are not reported in the registry record.

The findings do not establish that every secondary outcome changed in the same way. Outcomes differ in their definitions and follow-up periods, and multiplicity handling is not reported. The results for the primary endpoint cannot be extended automatically to later events, length of stay, quality of life, or all aspects of safety.

The record identifies this study as terminated but does not report the reason. That status should not be interpreted as evidence for or against the findings. The registry information also does not provide all details needed to evaluate missing data, the original design assumptions, or the full statistical plan. Those omissions constrain how completely the results can be independently assessed.

These statistics describe a comparison in the trial’s recorded population and care context. They do not answer every question about outcomes in other settings or populations. They are not medical advice and should not be interpreted as a recommendation about treatment.

18. Why This Trial Matters Statistically

This trial illustrates why readers should distinguish an absolute event-proportion comparison from a sponsor-reported hazard-ratio analysis. Both can describe the same randomized groups while answering related but non-identical statistical questions. Reporting the estimates, intervals, and methods separately makes the scale and uncertainty of each result clearer.

It also shows why the endpoint definition matters. The primary outcome combines worsening heart failure and all-cause death through a fixed follow-up window, with worsening heart failure tied to escalation of treatment or support. A single composite percentage is useful for a broad summary but cannot reveal the contribution of each component unless those component results are separately reported.

Open-label allocation, central event adjudication, and the Full Analysis Set are important features of the record, but they do not replace information about randomization procedures, missing-data handling, or the complete analysis plan. Those details help readers judge whether the posted estimates could be affected by measurement, attrition, or analytic choices.

Finally, multiple secondary outcomes require disciplined interpretation. Their patterns may add context, but without a reported multiplicity strategy their p-values should not be treated as independent confirmatory evidence. The trial is a useful example of reading estimates together with their definitions, uncertainty, analysis methods, and reporting limitations rather than relying on a single significance label.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves several trial-specific questions unresolved. It records a terminated status but does not report the reason for termination. It also does not report the original sample-size justification, whether the planned enrollment or endpoint strategy changed, or whether interim analyses were conducted. The sample-size illustrations based on observed effects do not fill those gaps.

The primary outcome population is named as the Full Analysis Set, but its exact membership rules are not reported. Missing-data methods, handling of participants without complete follow-up, and sensitivity analyses are also not reported in the registry record. The secondary outcomes have differing analyzed participant counts, without a complete explanation of all differences.

The study was open-label. A central committee is reported for adjudication of the worsening-heart-failure endpoint, but the registry record does not describe the committee’s procedures or clarify whether assessors for other outcomes were masked. The record also does not provide enough details to independently reproduce the sponsor’s primary analysis from the posted summary results.

Not all listed secondary outcomes have detailed numerical results in the record. A multiplicity strategy for the secondary analyses is not reported, limiting the confirmatory interpretation of their test results. The safety information includes event counts and listed terms, but does not provide a complete account of attribution or an arm-specific breakdown for each listed serious-event term. These limitations affect interpretation of the record; they do not by themselves establish that the analyses are biased or invalid.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effect of Serelaxin Versus Standard of Care in Acute Heart Failure (AHF) Patients — NCT02064868.
• Registry record last updated 2019-03-22; status last verified 2018-12.
• Results first posted 2019-03-22.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a randomized, open-label, parallel-group Phase 3 study of serelaxin plus standard of care versus standard of care alone in people hospitalized for acute heart failure. Serelaxin was administered as a continuous intravenous infusion at 30 µg/kg/day for 48 hours. Enrollment was 2666, and the recorded status is terminated.

The primary outcome was worsening heart failure or all-cause death through Day 5 in the Full Analysis Set. The posted arm percentages were 4.95% and 6.94%; the registry-reported analysis gave a hazard ratio of 0.71 with a 95% confidence interval from 0.51 to 0.98 and p = 0.017. A separate unadjusted recalculation gives a risk difference of 0.020 with a 95% confidence interval from < 0.001 to 0.039.

Secondary outcomes cover heart-failure events, symptoms, renal deterioration, length of stay, adverse events, and quality of life. Interpretation is limited by unreported details on multiplicity, missing-data handling, original design assumptions, and the reason for termination.