Reducing Decompensation Events Utilizing Intracardiac Pressures in Patients With Chronic Heart Failure (HF) (REDUCEhf): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Reducing Decompensation Events Utilizing Intracardiac Pressures in Patients With Chronic Heart Failure (HF) (REDUCEhf) (NCT00354159), a randomized na study. The primary outcome is Relative Risk Reduction of All Heart Failure Related Events in the Treatment Group Compared to the Control Group.

2. Clinical Question

The research question concerns a strategy for using device-measured heart pressures in heart-failure management, rather than the effect of a medication. The treatment group’s distinguishing feature was that physicians could use the monitor information in decisions about management; in the control group, they could not. Thus, the comparison addresses the management approach as a whole, not simply whether the device could measure pressure.

The registry describes the implantable monitor as an investigational device and also describes its use in combination with an implantable cardioverter defibrillator. It does not report enough detail to characterize which participants received which device configuration or how device information translated into particular clinical decisions. Those implementation details are not reported in the registry record.

3. Trial Design

REDUCEhf (NCT00354159) was a completed, randomized, single-masked, parallel-group device trial. The registry lists the phase as not applicable and reports enrollment of 442. The study began in 2006-04, and primary completion was in 2011-01. The sponsor was Medtronic Cardiac Rhythm and Heart Failure.

The treatment arm gave physicians access to device-based hemodynamic monitor information to guide patient management. The control arm did not give physicians access to that information for management. The intervention description identifies an implantable hemodynamic monitor (Chronicle IHM) and the monitor in combination with a single-chamber ICD (Chronicle ICD). The registry’s brief summary says the monitor records and reports heart pressures, while the combination device also has an ICD function. The specific allocation of device configurations among participants is not reported in the registry record.

The primary outcome was defined for all randomized subjects and compared the rate of heart-failure-related events over the 12-month post-implant randomized follow-up period. The primary outcome counts events including hospitalizations longer than 24 hours, shorter hospitalizations with intravenous therapy, emergency-department visits with intravenous therapy, and urgent clinic visits with intravenous therapy. The registry gives primary-outcome counts of 202 in the Treatment Arm and 198 in the Control Arm.

Details that would further characterize the design—including the masking procedures, the original sample-size justification, and whether interim analyses were planned—are not reported in the registry record. The same applies to further detail on how the device configurations were assigned and how physicians were instructed to respond to pressure readings.

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: Enrolled subjects were required to have a successful implant of the Chronicle® device prior to randomization. 407 subjects had an attempted implant of the Chronicle® ICD (Implantable Cardioverter Defibrillator) (406) or Chronicle IHM (Implantable Hemodynamic Monitor) (1 subject). Of these 407 subjects, 400 were randomized.

Randomized Study Period

Reasons for not completing this period:

Long-term Follow-up

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All 406 subjects with an attempted implant of the Chronicle ICD system.

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 Relative Risk Reduction of All Heart Failure Related Events in the Treatment Group Compared to the Control Group, measured over 12 months post-implant.

The primary endpoint is the rate of heart-failure-related events per year during the 12-month post-implant randomized follow-up period. The registry defines qualifying events as hospitalizations longer than 24 hours, hospitalizations shorter than 24 hours with intravenous therapy, emergency-department visits with intravenous therapy, and urgent clinic visits with intravenous therapy. The primary population is all randomized subjects.

An event rate expresses the number of qualifying events relative to the time participants contribute to follow-up. Unlike an outcome that records only whether a participant had any event, a rate can reflect repeated events in the same participant. That makes it a way to describe the overall burden of recurring events during follow-up. The registry’s primary outcome is therefore a comparison of event rates, not simply a comparison of the proportion of participants with at least one event.

General: A rate endpoint can be useful when events may recur and participants may contribute different amounts of observation time. Its interpretation depends on the event definition and the exposure period. Here, the registry specifies both the types of qualifying event and the 12-month randomized follow-up timeframe. It does not provide additional detail in the record about handling incomplete observation time or missing event information.

The endpoint is intended to capture a range of heart-failure-related healthcare encounters, from hospitalizations to urgent outpatient care, subject to the stated criteria. It does not by itself describe the severity of every event, the reasons for individual treatment decisions, or patient experience outside the defined events.

7. Results Posted in the Registry

• Treatment Arm: 0.48 versus 0.49 (Heart failure related events per year) on control; rate ratio 0.98 (95% CI 0.73–1.32, derived from the posted confidence limits); p ≈ 0.891.

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.

Relative Risk Reduction of Cardiovascular Related Events in the Treatment Group Compared to the Control Group

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, with the standard error taken from the posted confidence limits.
• Result:
  • Treatment Arm: 0.77 versus 0.86 (Cardiovascular related events per year) on control; rate ratio 0.90 (95% CI 0.71–1.13, derived from the posted confidence limits); p ≈ 0.347.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Treatment Arm and the control. The interval gives the range of effects that remain compatible with the data.

Characterize Randomized Days Alive Out of Hospital

• 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:
  • Treatment Arm: mean 340.00 versus 341.00 on control; difference -1.00 (95% CI -13.54 to 11.54), standardized effect d = -0.02; z-test p = 0.876.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Treatment Arm and the control. The interval gives the range of effects that remain compatible with the data.

Characterize Medication Usage

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • Treatment Arm: 1.77 versus 1.49 (Medication changes per subject month) on control; rate ratio 1.19 (95% CI 1.14–1.24, approximate, Poisson model); p ≈ <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically higher for Treatment Arm than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the description beyond the primary heart-failure-related event rate. They include cardiovascular-related events, days alive out of hospital, medication changes, survival and hospitalization measures, resource use, and other measures. Across the posted summaries, the secondary results do not form a uniform pattern of clear separation between groups. Some comparisons are imprecise or show little separation in their arm-level summaries, while the medication-change analyses illustrate that the result can depend on the method used.

These outcomes are related to the primary question but do not directly replace it. Cardiovascular-related events cover a different event category, days alive out of hospital captures time outside hospital, and medication changes describe care activity. They may provide context about different dimensions of the management strategy, but differences in endpoint definition and statistical method make them distinct questions.

Unadjusted secondary results carry less weight because many outcomes are examined. General: When multiple hypotheses are tested, the chance of seeing at least one nominally striking result by chance increases unless the analysis plan accounts for the number and structure of comparisons. The registry lists numerous outcome measures and analyses, but a multiplicity adjustment or testing hierarchy is not reported in the registry record. Therefore, an isolated secondary p-value should not be interpreted as confirmatory evidence on its own.

The secondary outcomes are most useful as descriptive context alongside the primary result. Their interpretation depends on the outcome definitions, follow-up, and methods used. The registry record does not report enough detail to determine whether all secondary analyses were prespecified or how they were prioritized.

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

• Cumulative Days in the Hospital for Heart Failure
• Relative Risk Reduction of Cardiovascular Related Events in the Treatment Group Compared to the Control Group
• Freedom From All Cause Death or Heart Failure Hospitalization
• Relative Risk of All-cause Events
• Percentage of Randomized Subjects at Each Level of the Composite Response Endpoint Between the Treatment Arm and the Control Arm.
• Characterize Health Resource Utilization
• Characterize Randomized Days Alive Out of Hospital
• Characterize Subject Survival

9. Statistical Interpretation

10. Statistical Methods Explained

General statistical explanation: The endpoint is a rate, which relates event counts to time under observation. A rate ratio compares the event rate in one group with the rate in another. A rate ratio of one represents equal rates; values on either side represent different relative rates. A rate ratio is not an absolute difference in the number of events, and it does not indicate how many individual participants experienced an event.

What does the recalculated comparison represent?

The recalculated primary comparison uses posted arm-level rates and their confidence intervals to produce an unadjusted rate-ratio estimate and interval. This is a simple comparison of the summary statistics, not a reproduction of the sponsor’s full analysis. Its unadjusted p-value is 0.891. Because the recalculation does not incorporate unreported participant-level information or model details, it should be interpreted as a descriptive statistical check rather than as a replacement for the registry’s reported analysis.

The primary outcome is a recurrent-event rate, so a participant may contribute more than one qualifying event. General: A simple count-based rate analysis commonly relies on assumptions about event counts and exposure. If the observed variability in counts is greater than the model assumes—known as over-dispersion—standard errors and confidence intervals may be too small unless the analysis accounts for that extra variability. The registry’s arm-level data identify the recalculation as Poisson-based, but the record does not report diagnostic checks or additional adjustment for over-dispersion.

What is the sponsor’s Andersen-Gill result?

The registry reports an Andersen-Gill analysis for the primary outcome and gives its result as a hazard ratio of 0.99, with a 95% confidence interval from 0.61 to 1.61 and p = 0.978. An Andersen-Gill approach is used for recurrent-event time-to-event data. It incorporates event timing and follow-up information in a way that differs from a comparison based only on the posted arm-level rates. The registry record does not give enough methodological detail to reconstruct that model, including its covariates or all assumptions.

A hazard ratio and a rate ratio are different measures. The hazard ratio relates instantaneous event rates over time under the model; the recalculated rate ratio compares aggregate rates over the specified period. Their numerical estimates need not match, and the two confidence intervals should be interpreted in relation to their own measures. Both reported primary comparisons have intervals spanning their respective no-difference values.

How should p-values be read?

General: A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the analysis assumptions were correct. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The unadjusted recalculated primary p-value is 0.891; the sponsor’s reported primary p-value is 0.978. Neither is evidence of a statistically clear difference under conventional testing, but neither proves equality.

The word “unadjusted” matters because the recalculated p-value does not account for the sponsor’s model or possible covariates. The sponsor’s reported primary result is tied to the Andersen-Gill analysis. Further details of the analysis plan, including any prespecified testing hierarchy, are not reported in the registry record.

What do secondary outcome methods add?

The secondary outcomes use more than one type of measure. Cardiovascular-related events and medication changes are expressed as rates, while days alive out of hospital is expressed as a mean with a standard deviation. General: A mean difference describes the difference in average values between groups; a rate ratio compares rates. A confidence interval communicates a range of effect estimates that are compatible with the data and the model at the stated confidence level.

The medication-change comparison has a recalculated rate-ratio estimate and an unadjusted p-value, while the sponsor’s analysis is described as negative-binomial regression and reports a different p-value. The analyses use different methods; the registry does not provide enough detail to reconcile their results. Negative-binomial regression is commonly used for count outcomes when event counts vary more than a basic Poisson model allows. This general rationale does not establish which assumptions held in this trial.

The posted planning illustrations use the observed effect as a reference and show sample sizes for different fractions of that effect. General: Such illustrations depend on assumptions about the target effect, statistical threshold, allocation, and model approximation. They are prospective planning calculations, not evidence about the trial’s actual ability to detect an effect after data collection.

Across outcomes, the registry reports several analyses and does not report a complete statistical analysis plan or multiplicity procedure. Consequently, isolated secondary p-values should be treated as exploratory unless the registry record establishes otherwise. The record does not establish a prespecified hierarchy for interpreting the secondary outcomes.

11. Confidence Intervals and Precision

A confidence interval describes the range of effect values compatible with the observed data under the analysis and its assumptions. It is not a guarantee that the true value lies inside the particular interval, and it does not remove uncertainty about the model or the quality of the data. Its width gives a sense of statistical precision: a wider interval leaves more plausible values unresolved.

For the recalculated primary rate ratio, the interval extends from 0.729 to 1.317. It includes one, the no-difference value for a rate ratio. Thus, the recalculation does not narrowly determine whether the relative rate is lower or higher in the Treatment Arm, nor does it tightly specify the magnitude of a possible difference.

The sponsor’s primary Andersen-Gill hazard-ratio interval is 0.61 to 1.61. It also includes one, the no-difference value for a hazard ratio, and spans a broad range of relative effects. The two intervals apply to different statistical measures and should not be read as if they were estimates from the same model. Their shared feature is that each leaves no-difference and effects in either direction compatible with the analysis.

General: A confidence interval’s width is influenced by the amount of information in the data, the variability of the outcome, and the analysis method. A p-value alone does not show this degree of precision. The primary p-values are not small, but the intervals are also important because they demonstrate that the estimates do not rule out a range of possible effects.

The registry gives arm-level confidence intervals for the primary rates and a confidence interval for the sponsor’s hazard ratio. The record does not report further details about how missing observations or incomplete follow-up affected precision. Therefore, the intervals quantify uncertainty under the reported analyses, not every source of uncertainty relevant to interpretation.

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 express their figures as participants per arm for 80% power and participants per arm for 90% power. They are not total event counts: the posted assumption says that only time-to-event planning figures use total events, while the other figures use participants per arm. The figures use equal allocation between two arms and a two-sided significance level of 0.05, with a normal approximation. They use the observed effect as a reference and consider detecting the stated fraction of that effect.

The 80% power column gives the illustrative number of participants per arm for a design that would have an 80% chance of meeting the specified statistical criterion if the assumed effect and planning assumptions were correct. The 90% power column gives the corresponding illustration for a 90% chance. These are planning concepts, not descriptions of what happened in REDUCEhf. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

The rows distinguish planning for 100%, 75%, and 50% of the observed effect. Across those scenarios, smaller effects require more participants per arm to maintain the stated power. That is because a smaller separation between groups is harder to distinguish from random variation. The primary endpoint’s illustrations are especially large relative to the randomized arm counts, reflecting the small observed rate difference used as the planning reference; the figures should not be read as a retrospective judgment about the trial.

These are planning illustrations, not observed power. They do not tell readers the probability that the trial’s null hypothesis is true, and they cannot establish whether an observed result is important. The original design rationale, including the effect the investigators intended to detect, is not reported in the registry record.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 0.4900; treatment rate λ₁ = 0.4800 events per patient-year; follow-up T = 1.00 years.
2. n = (1.96 + 0.842)² × (1/0.4900 + 1/0.4800) / (1.00 × [ln(0.980)]²) = 76,136.8, rounded up to 76,137 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
lambda0 <- 0.49                      # control rate, events per patient-year
lambda1 <- 0.48                      # treatment rate
tt      <- 1                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(354159)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 76,137 (80% power), 101,926 (90% power)
 75% of observed effect: n per arm = 135,003 (80% power), 180,731 (90% power)
 50% of observed effect: n per arm = 302,970 (80% power), 405,591 (90% power)
Simulated power, Poisson counts, n = 76,137 per arm: 0.800
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.629

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as an Andersen-Gill model, with a hazard ratio of 0.99, a 95% confidence interval from 0.61 to 1.61, and p = 0.978. The recalculated comparison from the posted arm-level primary rates is an unadjusted rate-ratio analysis, with an unadjusted p-value of 0.891. The estimates arise from different methods and measure different aspects of recurrent events, so they should not be expected to be numerically identical.

Both analyses indicate substantial uncertainty and do not establish a statistically clear difference between the groups on the primary outcome. The sponsor analysis uses the named time-to-event method, whereas the recalculation uses summary rates and a simple unadjusted comparison. The recalculation is useful as a check on the direction and broad scale of the posted arm-level figures, but it cannot reproduce the sponsor’s model from summary data alone.

For medication changes, the registry reports negative-binomial regression with p = 0.145, while the unadjusted rate-based recalculation gives p < 0.001. The record does not provide enough detail to determine why these analyses differ, including the specific model specification or data handling. This contrast illustrates why a summary-statistic recalculation should not be treated as a substitute for a sponsor analysis using a different model. The registry does not identify the recalculation as the sponsor’s prespecified analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 21 outcome measures and 16 analyses, including multiple secondary outcomes. It does not report a multiplicity adjustment or a hierarchy specifying which secondary comparisons should be treated as confirmatory. General: If many statistical tests are conducted, the chance of at least one result crossing a conventional significance threshold by chance can rise. An adjustment or prespecified hierarchy can help control interpretation, but whether one was used is not reported in the registry record.

The record identifies all randomized subjects as the primary outcome population. It does not give further detail about exclusions, the handling of participants who did not complete follow-up, or the treatment of missing event information. A detailed missing-data strategy is not reported in the registry record. It is therefore not possible to determine from the record whether missing outcome data were imputed, handled through a particular censoring approach, or addressed in sensitivity analyses.

The trial is described as randomized and single-masked, but the procedures used to maintain masking and the groups of people masked are not reported in detail. The original sample-size justification, interim-analysis plans, and full statistical analysis plan are also not reported in the registry record. These omissions limit assessment of whether every analysis was prespecified and how the analysis choices were made.

These reporting gaps do not by themselves show that a particular procedure was or was not used. They mark what cannot be established from the registry record. Interpretation should remain anchored to the posted endpoint definitions and analyses, while recognizing that missing-data handling, multiplicity control, and other protocol details are not described.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

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 (31.8%), renal failure acute (9.1%), angina pectoris (6.9%), ventricular tachycardia (5.6%), atrial fibrillation (5.1%).

For the randomized groups, the registry reports serious adverse events affecting 123 of 202 participants in the Treatment Arm and 136 of 198 in the Control Arm. Other adverse events affected 24 of 202 in the Treatment Arm and 25 of 198 in the Control Arm. The record also lists 8 serious adverse events among 42 enrolled participants who were not randomized, and no other adverse events in that group. These are counts of affected participants as recorded in the registry, not comparisons adjusted for follow-up or exposure.

The listed serious adverse event terms include cardiac failure at 31.8%, acute renal failure at 9.1%, angina pectoris at 6.9%, ventricular tachycardia at 5.6%, atrial fibrillation at 5.1%, and pneumonia at 4.0%. The registry does not provide the additional context needed to interpret these term percentages as comparative risks between randomized groups. Adverse-event counts alone do not establish that an event was caused by the device or management strategy.

Death counts are not reported in the registry record. The record’s adverse-event figures should be read as descriptive safety reporting; they do not replace a formal comparison of risk or explain the timing, seriousness criteria, or causal attribution for individual events.

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

The primary result describes the comparison of defined heart-failure-related event rates during the 12-month randomized follow-up. The arm-level rates are close, and both the recalculated rate-ratio interval and the sponsor’s hazard-ratio interval include their respective no-difference values. The analyses therefore do not establish a statistically clear difference between the randomized groups on the primary endpoint.

That conclusion is narrower than saying the groups were identical. The intervals leave a range of relative effects compatible with the data, so the result does not precisely determine the direction or size of any underlying difference. A non-significant test does not prove equivalence, and the registry does not report an equivalence or non-inferiority framework for this comparison.

The result also concerns access to device-based pressure information as part of clinical management, not just the technical ability of an implant to measure pressure. It does not isolate the effect of the monitor from all related management decisions, nor does the registry provide enough detail to characterize how physicians used the readings. The outcome is limited to specified healthcare encounters involving heart failure and does not encompass every aspect of health or care.

Secondary outcomes provide additional descriptive information, but their multiplicity and differing methods mean that they should not be used to override the primary result. The record does not report a multiplicity plan that would establish confirmatory status for secondary comparisons. Nor does it include enough detail on missing data, analysis populations beyond the stated primary population, or model specifications to resolve all uncertainties.

Accordingly, the posted findings support a careful statistical statement: the primary analyses did not demonstrate a clear group difference, and their precision leaves meaningful uncertainty. They do not establish that the intervention is beneficial, ineffective, equivalent, or harmful. Clinical decisions require broader evidence and judgment and are not determined by these registry statistics alone.

18. Why This Trial Matters Statistically

REDUCEhf raises a recurring statistical challenge in clinical research: how to compare strategies intended to influence events that may happen repeatedly over follow-up. The primary endpoint is an event rate, and the registry reports both arm-level rates and a recurrent-event time-to-event analysis. Understanding that these are related but different measures helps prevent an unadjusted summary comparison from being mistaken for a full model-based analysis.

The trial also shows why a confidence interval matters alongside a p-value. The primary analyses do not provide a statistically clear separation, but their intervals remain broad. The data therefore support neither a precise estimate of no effect nor a tight estimate of a difference. Distinguishing absence of clear evidence from evidence of equivalence is central to interpreting clinical trial results.

Another statistical lesson is the dependence of conclusions on endpoint and model choices. The trial includes event rates, time-to-event analysis, days alive out of hospital, and medication changes. Those outcomes capture different aspects of care and use different statistical methods. The medication-change results particularly illustrate that a summary-based recalculation and a sponsor model may yield different statistical conclusions when their methods differ.

Finally, the number of outcomes makes multiplicity and prespecification important. Without a reported testing hierarchy or adjustment, secondary findings should be considered in context rather than treated as independent confirmations. The registry’s omissions regarding missing-data procedures and original sample-size rationale also show how reporting detail affects the strength of statistical interpretation.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The registry record leaves important design and analysis details unspecified. Although it identifies the trial as randomized, single-masked, and parallel-group, it does not describe the masking procedures or who remained masked. It does not explain the original sample-size justification, planned interim analyses, or full statistical analysis plan. These gaps limit assessment of the prespecification and conduct of the analyses.

The primary comparison is based on recurrent heart-failure-related events, but the record does not provide participant-level event histories or detailed information on event timing and follow-up completeness. The recalculation relies on posted summary statistics and cannot reproduce the sponsor’s Andersen-Gill model. Model covariates, diagnostic checks, and details of handling incomplete observation are not reported in the registry record.

The device description includes both an implantable monitor and a monitor combined with an ICD, but the record does not explain the allocation or use of these configurations in enough detail to distinguish their contributions. It also does not describe in detail how physicians interpreted or acted on pressure information. Consequently, the comparison is best understood as a management strategy contrast rather than an isolated measurement-device effect.

There are multiple secondary outcomes, but a multiplicity procedure and the status of those analyses as prespecified or exploratory are not reported. Missing-data methods and sensitivity analyses are also not reported. These are limitations of what can be assessed from the registry record; they do not establish that the trial lacked such procedures.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Reducing Decompensation Events Utilizing Intracardiac Pressures in Patients With Chronic Heart Failure (HF) (REDUCEhf) — NCT00354159.
• Registry record last updated 2012-08-09; status last verified 2012-08.
• Results first posted 2012-08-09.
• 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

REDUCEhf (NCT00354159) was a completed, randomized, single-masked, parallel-group study sponsored by Medtronic Cardiac Rhythm and Heart Failure. It enrolled 442 participants with heart failure. The intervention gave physicians access to implantable hemodynamic monitor information for management; control physicians did not have access to that information. The primary endpoint was the rate of defined heart-failure-related events per year over 12 months post-implant.

The posted primary arm-level rates were 0.48 in the Treatment Arm and 0.49 in the Control Arm. The sponsor reported an Andersen-Gill hazard ratio of 0.99 with a 95% confidence interval from 0.61 to 1.61 and p = 0.978. Neither the sponsor analysis nor the unadjusted rate-based recalculation establishes a clear difference. The intervals leave substantial uncertainty, and the registry does not report several design and analysis details relevant to interpreting that uncertainty.