Cardiac Rehabilitation Peer Mentorship: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cardiac Rehabilitation Peer Mentorship (NCT02204449), a randomized na study. The primary outcome is Cardiac Rehabilitation Enrollment.

2. Clinical Question

3. Trial Design

The registry describes a randomized controlled trial with parallel groups and single masking. The stated enrollment was 94. Participants were assigned to cardiac rehabilitation peer mentorship or usual care at two hospitals in Toronto, Ontario, Canada. The record lists the study as completed, with a start of 2014-07 and primary completion of 2015-01. The phase is listed as NA, consistent with a behavioral intervention rather than a drug-phase designation.

The intervention was a hospital visit from a trained cardiac rehabilitation peer mentor. The mentor was to explain cardiac rehabilitation, discuss its benefits, stress the importance of referral, and arrange a follow-up call. Usual care included health-provider and allied-health-professional care, without a peer mentor visit. The registry description does not establish that all elements of usual care were identical across participants or specify the duration and content of other clinical care.

The primary outcome was enrollment in cardiac rehabilitation by 12 weeks after discharge. A blinded research assistant was to determine enrollment from medical records or by calling the participant at home. Referral to cardiac rehabilitation was listed as a secondary outcome with the same general follow-up interval. The registry record lists 39.0 participants in the mentorship group and 37.0 in usual care for the primary outcome summaries. It does not explain how these outcome denominators relate to the stated enrollment of 94, or identify the analysis population used.

Random allocation is recorded, but the sequence-generation method, allocation concealment, and masking procedures beyond the single-masking designation are not reported in the registry record. The identity of the person or group masked is also not reported. The trial’s original sample-size assumptions, protocol deviations, and any interim analyses 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.

Overall Study

Reasons for not completing this period:

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 Cardiac Rehabilitation Enrollment, measured over 12 weeks after patient is discharged from hospital.

The primary endpoint is the number of participants enrolled in cardiac rehabilitation within 12 weeks after hospital discharge. The registry describes enrollment as a binary outcome: each participant is classified according to whether enrollment occurred. It was assessed by a blinded research assistant, who could examine medical records or call the participant at home.

Enrollment is distinct from referral. A referral is a step toward rehabilitation, while enrollment indicates that the participant entered the program. The trial therefore listed referral separately as a secondary outcome, allowing the two stages of engagement to be considered separately. These measures address the trial’s stated question about whether peer mentorship might encourage uptake of cardiac rehabilitation among cardiac inpatients.

Using a fixed follow-up interval gives the outcome a defined time window and makes the endpoint interpretable as enrollment by that point after discharge. It does not, by itself, show how long participants attended rehabilitation, whether they completed a program, or what later outcomes followed. Those outcomes are not reported in the registry record. The record also does not describe how conflicting information between medical records and participant reports was resolved, how unsuccessful contact attempts were handled, or whether endpoint ascertainment was complete for all randomized participants.

7. Results Posted in the Registry

• Cardiac Rehabilitation Peer Mentorship: 51.3% (20/39) versus 40.5% (15/37) on control; risk difference 10.7 percentage points (95% CI -11.5 to 33.0), risk ratio 1.26 (0.77–2.08); unadjusted two-proportion z-test p = 0.348.

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.

Cardiac Rehabilitation Referral

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Cardiac Rehabilitation Peer Mentorship: 79.5% (31/39) versus 73.0% (27/37) on control; risk difference 6.5 percentage points (95% CI -12.6 to 25.6), risk ratio 1.09 (0.85–1.40); unadjusted two-proportion z-test p = 0.504.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cardiac Rehabilitation Peer Mentorship and the control. The interval gives the range of effects that remain compatible with the data.

Cardiac rehabilitation referral is the named secondary endpoint. The posted point estimate for referral is positive in the mentorship direction, as is the primary enrollment point estimate. Thus the broad pattern is directionally aligned: the observed summaries do not show the two outcomes pointing in opposite directions. However, referral and enrollment describe different stages of participation, and one endpoint cannot be substituted for the other.

Both comparisons are imprecise, with confidence intervals that include differences in either direction. The secondary result therefore does not resolve the uncertainty around the primary result, nor does agreement in direction independently confirm an effect. The two outcomes are also likely to be related because referral may precede enrollment, so they should not automatically be treated as independent evidence.

The registry indicates 3 outcome measures, while the posted outcome details identify the primary enrollment endpoint and a named secondary referral endpoint. Details for any remaining outcome measure are not reported in the registry record. No secondary analyses are listed. The record also does not state whether a hierarchy of outcomes was prespecified or whether multiplicity adjustments were planned.

Unadjusted secondary results generally carry less weight than a prespecified primary result because examining multiple outcomes creates more opportunities for chance findings. Without a reported testing hierarchy or multiplicity plan, a secondary p-value should be treated as exploratory rather than as a separate confirmatory test. The appropriate interpretation is therefore an overall one: the secondary endpoint has a pattern broadly consistent with the primary point estimate, but it adds limited certainty and does not remove the imprecision or reporting gaps surrounding the main comparison.

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

• Cardiac Rehabilitation Referral

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports binary outcomes as counts of participants with the event. For this trial, the primary event is enrollment in cardiac rehabilitation within 12 weeks after discharge. A participant either had the event during the defined period or did not. The group counts form the basis for comparing the observed event proportions.

What does a risk difference express?

A risk difference subtracts the event proportion in the comparator group from the event proportion in the intervention group. A positive value means the observed event proportion is higher in the intervention group; a negative value means it is lower. The reported primary risk difference is 0.107. This estimate describes the observed contrast and is not, by itself, a guarantee that the same contrast would occur in another sample or setting.

Unlike a relative measure, a risk difference keeps the contrast on the event-proportion scale. It can therefore be read as the absolute separation between the two group proportions. The risk difference does not say how many additional participants would enroll in a different-sized population, and no new population count should be inferred without a clearly specified population size and assumptions.

How should the confidence interval be read?

A confidence interval gives a range of values reasonably compatible with the data under the method used to calculate it. In repeated use of a valid interval procedure, intervals constructed in this way would cover the underlying parameter at their stated confidence level at the procedure’s long-run rate. It is not a probability statement that the particular unknown effect lies in the displayed interval after the data have been observed.

The primary interval runs from -0.115 to 0.330. Because it extends across zero, the posted data are compatible with a negative difference, little or no difference, and a positive difference. Its width signals that the estimate is not precise enough to sharply distinguish among these possibilities. A point estimate should therefore be read together with its interval rather than as a standalone conclusion.

What does the p-value add?

The unadjusted p-value is 0.348. In general, a p-value is calculated under a null hypothesis and measures how unusual data at least as incompatible with that null would be, given the test’s assumptions. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result occurred by chance. A p-value also does not describe the size or practical importance of an effect. For interpretation, it is best considered alongside the estimated difference, its confidence interval, the design, and the completeness of the data.

The registry lists risk ratios and odds ratios as additional relative summaries. A risk ratio compares the event proportions, while an odds ratio compares the event odds. These measures answer questions on different scales from the risk difference and should not be treated as interchangeable. Their interpretation depends on the event frequency and the measure’s definition. The corresponding intervals are broad, consistent with uncertainty in the group contrast. No adjusted analysis is listed in the registry record.

What does randomization contribute?

Random assignment is intended to make the groups comparable, on average, with respect to factors that could affect the outcome. It supports a causal comparison when allocation, follow-up, measurement, and analysis are implemented appropriately. The record confirms randomization but does not report enough detail to assess sequence generation or concealment. It also does not report the analysis population, adherence to assigned groups, or handling of missing outcomes. Randomization alone cannot resolve uncertainty caused by limited outcome information or incomplete reporting.

Single masking is recorded, and the endpoint description specifically identifies a blinded research assistant. The record does not state who else was masked, or how masking was maintained. Blinded outcome assessment can reduce the opportunity for knowledge of group assignment to influence measurement, but the registry description does not allow a broader assessment of masking across trial conduct.

Why can over-dispersion matter in other outcomes?

General statistical explanation: for a binary endpoint summarized as a count, the main issue is uncertainty in the event proportions and their contrast. For outcomes measured as counts or rates, over-dispersion means observed variability exceeds what a simple model assumes. Ignoring it can make standard errors too small and confidence intervals too narrow. The posted primary endpoint is a binary participant count, and no over-dispersion parameter is reported for it.

The record lists no reported analyses for the secondary endpoint, and it does not provide a detailed statistical plan. Consequently, the precise test procedures, any covariate adjustment, treatment of clustering by hospital, and approach to multiple comparisons are not reported in the registry record. The displayed comparison statistics should be read as posted summary comparisons, not as a substitute for an unavailable full protocol or analysis report.

11. Confidence Intervals and Precision

The primary estimate is a risk difference of 0.107, with a confidence interval from -0.115 to 0.330. The interval is wide relative to the point estimate and crosses zero. This means the trial’s posted data do not locate the underlying group contrast precisely: values consistent with a lower enrollment proportion under mentorship and values consistent with a higher proportion remain within the interval.

Precision is affected by the amount of outcome information, the variability of the outcome, and the analysis method. The outcome summaries use denominators of 39.0 and 37.0. The registry record does not give a sample-size justification for the original trial or explain the relationship between these denominators and the stated enrollment of 94. It also does not report the completeness of outcome ascertainment. These gaps limit assessment of how the available endpoint data arose.

A confidence interval is not a range containing every plausible explanation or every result that could arise in a future trial. Nor does an interval that includes zero establish equivalence. An equivalence conclusion would require a prespecified margin and an analysis designed for that purpose; neither is reported in the registry record. Likewise, the interval should not be read as a prediction interval for a different hospital or population.

The referral estimate is also imprecise, with an interval spanning negative and positive differences. Considering both endpoints, the point estimates lean in the same direction, but neither interval identifies a narrow range of effects. The most defensible reading emphasizes this uncertainty rather than treating the direction of either point estimate as conclusive. More complete reporting of the analysis plan and outcome data would help readers assess precision and the robustness of the comparison.

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 figures are planning illustrations, not the trial’s original design calculation. For these binary outcomes, each figure is the number of participants per arm, not a total number of events. The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They set the effect to detect at the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column represents a planning target under which a study designed with the stated assumptions would have an 80% chance of detecting the specified effect at the chosen significance level, if that effect and the other assumptions were correct. The 90% power column represents a higher chance of detecting that same specified effect, under those assumptions. These are design targets, not guarantees for any particular study.

Each row uses a different fraction of the observed effect: the full observed effect, 75% of the observed effect, or 50% of the observed effect. The smaller the effect a future study is intended to detect, the more participants it generally needs, all else equal. The figures rise accordingly as the target effect becomes smaller, and the 90% target requires more participants per arm than the 80% target for a given effect assumption.

For example, planning for 100% of the observed primary effect gives 337 participants per arm for 80% power and 451 participants per arm for 90% power. These calculations use the observed estimate as a planning reference; they do not establish that the observed estimate is the true effect. This is not observed power. The illustrations are not evidence that the completed trial had a particular probability of detecting an effect, and they should not be used to infer the trial’s original design rationale.

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 = 0.405; treatment proportion p₁ = 0.513; average p̄ = 0.459.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7047 = 1.3813.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7006 = 0.5897.
4. n = (1.3813 + 0.5897)² / (0.1074)² = 336.7, rounded up to 337 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 <- 0.405405405405405                          # control proportion
p1 <- 0.512820512820513                          # 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(2204449)
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 = 337 (80% power), 451 (90% power)
 75% of observed effect: n per arm = 597 (80% power), 798 (90% power)
 50% of observed effect: n per arm = 1,335 (80% power), 1,786 (90% power)
power.prop.test: 336.7 
Simulated power at n = 337 per arm: 0.801 (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. Multiplicity, Missing Data and Analysis Populations

The registry names cardiac rehabilitation enrollment as the primary outcome and referral as a secondary outcome. It also records 3 outcome measures, although the posted outcome details name only one secondary endpoint in addition to the primary endpoint. The details for the remaining outcome measure are not reported in the registry record. The record does not describe a prespecified hierarchy among outcomes or explain which analyses were intended to support confirmatory conclusions.

Multiplicity arises when several outcomes, time points, subgroups, or statistical comparisons are examined. Without an appropriate plan, the chance of at least one apparently notable result can increase. Common approaches include defining a single primary test, specifying a testing order, or adjusting the interpretation of multiple tests. Which approach, if any, was planned for this trial is not reported in the registry record. No multiplicity adjustment is described for the posted secondary comparison.

Missing-data handling is also not reported. The record does not state whether all randomized participants had endpoint status determined, how missing medical records or unsuccessful telephone contact were handled, or whether any imputation or sensitivity analysis was used. The stated enrollment is 94, while the primary summaries list group denominators of 39.0 and 37.0. The record does not explain this relationship, so the available summaries do not establish how all enrolled or randomized participants were represented in the analysis.

The analysis population is not reported in the registry record. In particular, the record does not specify whether participants were analyzed according to randomized assignment, whether any participants were excluded after randomization, or how crossovers and deviations from assigned care were handled. These details matter because excluding participants or analyzing them differently from their assignment can alter the comparability created by randomization.

The endpoint description says that a blinded research assistant assessed enrollment through medical records or a participant call. It does not report completeness checks, adjudication procedures, or the handling of disagreement between sources. These omissions do not demonstrate that the conduct was inadequate; they limit what can be concluded from registry reporting alone.

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

The posted primary data show more recorded enrollment events in the mentorship group than in usual care, and the estimated risk difference is positive. The estimate is accompanied by a confidence interval that spans both negative and positive differences. The result therefore supports a descriptive statement about the observed groups but does not precisely establish the size or direction of the underlying difference.

A p-value above a conventional threshold is not evidence that the groups are equivalent, and it is not proof that mentorship has no effect. Equivalence requires a prespecified range of differences that would be considered sufficiently small, along with an appropriate design and analysis. Such a margin is not reported in the registry record. Conversely, a positive point estimate does not establish that mentorship increases enrollment in a broader population. The interval and the trial’s reporting limitations need to remain part of the interpretation.

The findings concern enrollment within 12 weeks after hospital discharge at the participating Toronto hospitals. They do not directly describe longer-term attendance, completion of cardiac rehabilitation, or clinical outcomes after rehabilitation. Those outcomes are not reported in the registry record. The reported follow-up window and settings also limit how directly the estimate can be applied to other populations or care systems.

The secondary referral endpoint is relevant to the proposed pathway from peer discussion to rehabilitation participation, but referral is not the same as enrollment. Its directional pattern is consistent with the primary point estimate, while its uncertainty means it cannot settle the primary question. Nor does the registry evidence establish that any observed difference was caused solely by the mentor visit; the record lacks sufficient detail about implementation, other care, and analysis to assess all possible influences.

Accordingly, the result is best understood as an uncertain randomized comparison with a positive observed point estimate, not as proof of benefit, proof of no effect, or a clinical recommendation. The registry record does not report enough about the original statistical plan, missing data, or analysis population to support stronger conclusions.

16. Why This Trial Matters Statistically

This trial illustrates why effect estimates and confidence intervals are more informative than a simple focus on whether a p-value crosses a threshold. The primary estimate is positive, but the interval includes effects in both directions and is broad. The statistical story is therefore not captured by a yes-or-no label. Readers need to consider the observed direction, plausible range, and quality of reporting together.

It also illustrates the distinction between intermediate steps in a care pathway. Referral and enrollment are related but separate binary outcomes. Looking at both can describe whether the observed pattern is similar across stages, but multiple outcomes can complicate interpretation, particularly when the testing hierarchy is not reported. The registry identifies a secondary endpoint but does not explain a multiplicity plan.

The planning illustrations make another statistical distinction visible: the effect assumed for a future design drives the required sample size. Planning around a smaller effect requires more participants, and a higher power target also requires more participants. Because the observed effect is uncertain, these figures are examples for planning rather than a definitive design recommendation or a reconstruction of the trial’s original rationale.

Finally, the relationship between stated enrollment and the displayed endpoint denominators underscores the importance of participant flow and analysis-population reporting. A randomized design is valuable, but readers also need to know who was included in each analysis and how missing outcomes were addressed. The registry record does not provide those details. These are central statistical considerations for judging how much weight the posted comparison can carry.

17. 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 available registry information leaves several trial-specific limitations that affect interpretation. The stated enrollment is 94, whereas the primary outcome summaries use denominators of 39.0 and 37.0. The record does not explain the relationship between these numbers or provide a participant-flow account. It is therefore not possible from the registry record to determine why the outcome denominators differ from stated enrollment or how many participants had outcome status unavailable.

The original sample-size justification is not reported in the registry record. Although planning illustrations are available based on fractions of the observed effect, they are not the original design assumptions and cannot establish what difference the trial was designed to detect. The registry also does not report the random-sequence method, allocation concealment, the identity of all masked parties, or an analysis plan. Single masking and blinded endpoint assessment are noted, but their full implementation is not described.

The report does not provide demographic or clinical characteristics of participants, detailed eligibility criteria, or outcome results by hospital. It is therefore difficult to assess how representative the participants were or whether the observed results varied across the two sites. The description of usual care is broad, and the registry does not describe how consistently the intervention or comparator was delivered.

Missing-data procedures, the analysis population, protocol deviations, and sensitivity analyses are not reported. The registry lists 3 outcome measures but gives details for only the primary endpoint and one named secondary endpoint. It also does not describe any multiplicity plan or reported secondary analyses. Adverse-event group entries show 0 at risk and 0 affected in both groups, while deaths are listed as null; these entries do not provide enough information to characterize safety or exposure.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Cardiac Rehabilitation Peer Mentorship — NCT02204449.
• Registry record last updated 2015-12-30; status last verified 2015-11.
• Results first posted 2015-06-22.
• 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.

21. Record Summary

NCT02204449 is a completed, randomized, parallel-group, single-masked trial titled Cardiac Rehabilitation Peer Mentorship. It compared a hospital visit from a trained cardiac rehabilitation peer mentor with usual care among cardiac inpatients at two Toronto hospitals. Stated enrollment was 94; the primary outcome was enrollment in cardiac rehabilitation within 12 weeks after discharge.

The posted primary estimate is a risk difference of 0.107, with a 95% confidence interval from -0.115 to 0.330 and an unadjusted p-value of 0.348. The interval includes differences in either direction, leaving the size and direction uncertain. Referral was listed as a secondary endpoint, with a directionally similar but also imprecise comparison.

The registry record does not report the original sample-size assumptions, missing-data approach, analysis population, multiplicity plan, or a detailed statistical analysis plan. The relationship between stated enrollment and the outcome denominators is also not explained. These gaps limit interpretation beyond the posted endpoint summaries.