EWISE: Study of Eplerenone in Women With Chest Pain, Coronary Vascular Dysfunction and Evidence of Myocardial Ischemia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for EWISE: Study of Eplerenone in Women With Chest Pain, Coronary Vascular Dysfunction and Evidence of Myocardial Ischemia (NCT00187889), a randomized phase 4 study. The primary outcome is Epicardial Coronary Artery Endothelial Function (Adjusted) at Week 16 Comparing the Eplerenone Group to the Placebo Group.

2. Clinical Question

The question is specific to a population described as having ischemic symptoms and microvascular dysfunction without significant disease in the larger epicardial coronary arteries. The registry’s background statement proposes that small-vessel function may be abnormal in some women with chest pain and says the study sought to test whether eplerenone could improve that function and possibly chest pain. That description explains the rationale; it does not establish that a change in the physiological endpoint would translate into symptom improvement.

The registry also lists microvascular coronary flow reserve at 16 weeks as a secondary outcome. This gives the study a second vascular-function measure, distinct from the primary measure of epicardial response to acetylcholine. The record does not report a patient-reported chest-pain endpoint among the posted outcomes described in the results.

3. Trial Design

EWISE is recorded as a phase 4, randomized, double-blind, parallel-group, placebo-controlled study. The official title describes it as multicenter. The University of Florida is listed as sponsor, and the registry status is completed. Enrollment was 70. The recorded study start is 2004-08 and primary completion is 2009-02.

Participants were assigned to eplerenone or placebo. The eplerenone schedule was 25 mg daily for 1 week followed by 50 mg daily for 15 weeks. The placebo schedule was a blinded 25 mg tablet daily for 1 week followed by 2 pills daily for 15 weeks. The primary outcome timeframe was 16 weeks. The registry record does not report the randomization method, allocation concealment procedure, or details of how masking was maintained.

The primary outcome analysis includes 19 participants in the eplerenone group and 22 in the placebo group. The secondary outcome analysis includes 13 and 18 participants, respectively. These are the outcome-specific analysis counts in the posted results; the record does not explain why the counts differ from the enrollment figure or from one outcome to another. The participant flow, withdrawals, exclusions, and reasons for missing outcome measurements are not reported in the registry record.

The record gives a study-planning description for the primary outcome: the study planned to detect a 12% difference in change from baseline to 16 weeks, with an SD of 14%, and describes 22 participants per group for 80% power, with a final planned total of 50 to allow for 6 dropouts. The original statistical protocol, the basis for these assumptions, and whether the intended analysis was changed are not reported in the registry record. Those original design statements are distinct from the separate illustrative sample-size calculations based on the observed effect.

The listed analysis method for both posted sponsor analyses is a Satterthwaite corrected t-test. Details such as the exact model specification, analysis population, handling of missing measurements, and any prespecified 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.

Before assignment: A total of 70 participants were screened for the study. Out of the 70 participants a total of 18 screened failed, 1 patient was withdrawn due to developing a spasm during the provocative testing screening which was believed to represent thrombosis and was not randomized to the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: power analysis: Study planned to detect a 12% difference in change from baseline to 16 weeks between treatment groups (SD=14%), in the primary outcome leading to a planned sample size of 22 per group (44 total) for 80% power, P=0.05 2-sided. Study allowed for 6 dropouts, leading to a final N=50 planned (25 per group). Per protocol analysis used.

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 Epicardial Coronary Artery Endothelial Function (Adjusted) at Week 16 Comparing the Eplerenone Group to the Placebo Group, measured over 16 weeks.

The primary endpoint is described as epicardial coronary artery endothelial function at 16 weeks. It is based on the relative change in coronary artery diameter in response to acetylcholine, abbreviated ACH, with the comparison adjusted for baseline reactivity to acetylcholine. Diameter was measured in millimetres at baseline and at 16 weeks; the registry defines the endpoint as the percent change at 16 weeks minus the percent change at baseline. Its unit is described as a unitless percentage-change difference.

Acetylcholine is used in this endpoint as a stimulus for evaluating the vessel’s endothelial response. In general, a vascular response measure can provide a physiological indicator of endothelial function: it assesses how the vessel changes after a defined stimulus rather than relying only on symptoms or clinical events. The record’s adjustment for baseline reactivity is intended to account for the starting response when comparing groups at follow-up. The exact adjustment model is not reported in the registry record.

This endpoint addresses function in the epicardial coronary artery, the larger coronary vessel, while the study rationale also discusses dysfunction of microscopic coronary vessels. The secondary outcome, microvascular coronary flow reserve, is the outcome more directly named for microvascular function. These measures concern related but distinct aspects of coronary physiology. Neither is, by itself, a direct measure of chest-pain frequency, daily function, or a cardiovascular event. The registry does not report a direct symptom endpoint among the posted outcomes.

7. Results Posted in the Registry

• EPLERINONE: mean -1.20 versus -10.70 on control; difference 9.50 (95% CI -3.24 to 22.24), standardized effect d = 0.44; z-test p = 0.144.

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.

Microvascular Coronary Flow Reserve(Adjusted) at Week 16 Adjusted for Baseline Coronary Flow Reserve Comparing the Eplerenone Group to the Placebo Group

• 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:
  • EPLERENONE: mean -0.40 versus -0.40 on control; difference 0.00 (95% CI -0.74 to 0.74), standardized effect d = 0.00; z-test p = 1.000.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between EPLERENONE and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome: microvascular coronary flow reserve adjusted for baseline at 16 weeks. Its group summaries are centered at the same value, and the unadjusted comparison shows no separation in the estimated means. The uncertainty interval includes zero. At an overall level, this secondary result is consistent with the primary result in not showing a clear difference between the treatment groups on the posted vascular-function measures.

The outcomes are related in that both concern coronary vascular function, but they measure different aspects of physiology. The primary endpoint concerns epicardial coronary artery response to acetylcholine, whereas the secondary endpoint is explicitly named for microvascular coronary flow reserve. Similarity in their overall pattern does not make them interchangeable, and one result does not validate the other. The registry does not report a combined analysis or a prespecified hierarchy linking the two outcomes.

Secondary results generally carry less weight than the primary result when they are among multiple outcomes because repeated testing can increase the chance of findings that appear notable by chance. In general, adjustment for multiplicity or a prespecified testing sequence can address some of that concern. Whether the trial used a multiplicity adjustment, or specified a hierarchy for outcomes, is not reported in the registry record. The posted secondary finding should therefore be treated as supportive descriptive evidence rather than as a stand-alone confirmatory conclusion.

The available secondary analysis includes fewer participants than the primary analysis. The record does not explain the different counts or report whether missingness could have affected the estimate. That limits how confidently the secondary result can be compared with the primary result or generalized to all enrolled participants. No further secondary outcomes are reported in the registry record.

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

• Microvascular Coronary Flow Reserve(Adjusted) at Week 16 Adjusted for Baseline Coronary Flow Reserve Comparing the Eplerenone Group to the Placebo Group

9. Statistical Interpretation

10. Statistical Methods Explained

The registry lists a Satterthwaite corrected t-test for the sponsor-reported comparisons. A t-test evaluates a difference in group means relative to the amount of variability and the number of observations. The Satterthwaite correction is a general approach used when group variances may differ; it adjusts the degrees of freedom rather than assuming that both groups have identical variance. The exact implementation and model details are not reported in the registry record.

What does a mean difference represent?

A mean is the arithmetic average of the observed endpoint values in a group. The primary outcome is continuous, so the comparison is expressed as a difference between group means. A positive or negative sign depends on which group is subtracted from which. The registry’s reported contrast and the unadjusted recalculation use opposite orientations, which explains their opposite signs. The direction should therefore be read alongside the stated group order, rather than by treating the sign alone as evidence of benefit or harm.

The group summaries describe the spread of individual measurements using standard deviations. Standard deviation reflects how dispersed the observations are around a group mean; it is not the same quantity as the standard error of a mean or the uncertainty interval around a group difference. The primary standard deviations are 15.4 in the eplerenone group and 25.6 in the placebo group. The unequal spread is one reason a variance correction can be relevant. In general, when variability differs between groups, a method that allows for that difference can avoid relying on a pooled-variance assumption that may not fit the data well.

What does a confidence interval add?

A confidence interval gives a range of values compatible with the data and the specified analysis procedure. It communicates uncertainty in the estimated difference, rather than only whether a test crosses a threshold. A wide interval indicates limited precision: several materially different underlying effects may remain compatible with the observed data. An interval that includes zero does not prove that the true difference is zero; it means that no difference remains compatible with the data under that interval procedure. The confidence interval should be considered with the point estimate and the study’s design and analysis limitations.

How should the p-value be read?

A p-value is a measure of how unusual results at least as far from the null value would be under the test’s assumptions if the null hypothesis were true. It is not the probability that the null hypothesis is true, nor does it measure the clinical importance of a result. The primary recalculated p-value is 0.144, while the sponsor-reported primary p-value is 0.15. Both are read alongside the estimates and confidence intervals; neither, by itself, tells how large or important a difference might be.

The recalculated primary comparison is explicitly an unadjusted re-calculation from posted group summaries. It does not reproduce any adjustment beyond those summary statistics, and it should not be confused with the sponsor’s reported analysis. The endpoint description says that the primary measure was adjusted for baseline reactivity, while the registry’s listed method is a Satterthwaite corrected t-test. The precise relationship between the endpoint adjustment and the reported test is not detailed in the registry record. The recalculation is useful for interpreting the posted group-level results, but it cannot recover unreported model details or participant-level information.

Why can over-dispersion matter?

In general, over-dispersion means that observations vary more than a statistical model expects. For a continuous outcome, unequal or unexpectedly large variability can make standard errors and confidence intervals too small if the method assumes less variation than is present. A variance-robust or unequal-variance procedure can account for some forms of unequal group variability. The registry’s Satterthwaite corrected t-test is consistent with allowing unequal variances in a comparison of means, but the record does not report diagnostic checks or the full analysis specification. This general explanation does not establish whether over-dispersion was present in this trial.

What can the group counts tell us?

The primary results list 19 participants for eplerenone and 22 for placebo. The secondary results list 13 and 18. These counts identify the numbers contributing to the respective outcome summaries; they do not, on their own, show why other enrolled participants are not represented in a given analysis. The registry does not report a participant flow account, missing-data method, or analysis-population definition. It is therefore not possible to determine from the posted record whether analyses followed intention-to-treat principles, used available cases, or applied another approach.

For general interpretation, randomized assignment supports a treatment-group comparison when the analysis preserves the randomized groups and missing outcomes do not undermine comparability. Missingness can be consequential if its occurrence or pattern is related to treatment or endpoint values. Without details about withdrawals, outcome availability, and analysis populations, the extent of any such concern cannot be assessed. The reported counts and results remain informative descriptions of the analyzed observations, but the registry record does not give enough detail to evaluate all assumptions behind the comparisons.

11. Confidence Intervals and Precision

The primary recalculated mean difference is 9.5, with a 95% confidence interval from -3.243 to 22.24. The point estimate is only one estimate among a range of values compatible with the data. Because the interval crosses zero, the results do not rule out no group difference. The interval also reaches positive and negative values, so the direction of the underlying difference is uncertain. It is not appropriate to interpret the point estimate as a precise or definitive treatment effect.

The sponsor-reported primary interval is -22.8 to 3.6 for its contrast orientation. It likewise includes zero. The reversed sign compared with the recalculation reflects contrast ordering, not a second, independent finding. The sponsor’s result and the recalculation are based on different presentations of the comparison, and the sponsor’s method is the registry-reported analysis.

Confidence intervals are useful because they show both the estimate and its statistical uncertainty. In general, a narrower interval indicates greater precision, while a wider interval leaves more plausible values unresolved. Precision depends on factors including the amount of variability and the number of observations. The outcome-specific group counts are modest, and the endpoint values show substantial spread, particularly in the placebo group. The registry’s confidence interval therefore deserves attention as an indication that the data do not pin down the primary difference closely.

The interval is not a range that contains the true effect with a guaranteed probability for this particular trial, and it does not assign probabilities to individual effect values. Nor does an interval including zero show that every clinically meaningful effect has been excluded. The registry record does not state a threshold for a clinically important difference, so statistical uncertainty cannot be translated into a judgment about clinical importance. Interpretation should remain tied to the endpoint measured, the population analyzed, and the limitations in the record.

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 concern participants per arm, not total event counts. They are based on a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is defined as a stated fraction of the observed effect. The figures are planning illustrations computed from the observed effect, not the trial’s original sample-size justification. The original design assumptions are described separately in the registry record; further details about their derivation are not reported.

For the full observed effect, the illustration gives 81 participants per arm for 80% power and 108 participants per arm for 90% power. For planning for 75% of the observed effect, it gives 143 participants per arm for 80% power and 192 participants per arm for 90% power. For planning for 50% of the observed effect, it gives 322 participants per arm for 80% power and 431 participants per arm for 90% power.

In general, a power target describes the chance that a study will detect an effect of the specified size under the assumptions used, if that effect is present. The 80% and 90% columns are alternative planning targets: the higher target calls for a larger planned sample under the same assumptions. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm when the effect used for planning is smaller. These values are not observed power; they are planning calculations based on the observed effect and stated assumptions.

The calculations should not be read as a recommendation or as a reconstruction of the original trial design. The observed effect is uncertain, and a planning illustration inherits that uncertainty. A different assumed effect, variability, analysis method, or design could lead to different sample-size requirements. The registry does not report the assumptions underlying every aspect of the original design beyond its stated planning description.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 9.500; pooled standard deviation σ = 21.502.
2. n = 2 × (1.96 + 0.842)² × 21.502² / 9.500² = 80.4, rounded up to 81 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 9.5                      # observed difference in means
sigma <- 21.5022002451985                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(187889)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 81 (80% power), 108 (90% power)
 75% of observed effect: n per arm = 143 (80% power), 192 (90% power)
 50% of observed effect: n per arm = 322 (80% power), 431 (90% power)
power.t.test: 81.4 
Simulated power at n = 81 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor-reported primary analysis is a Satterthwaite corrected t-test. It gives a net mean difference of -9.6, with a 95% confidence interval from -22.8 to 3.6 and p = 0.15. The unadjusted recalculation from the posted group summaries gives a mean difference of 9.5, a 95% confidence interval from -3.243 to 22.24, and p = 0.144. The sign differs because the contrast is expressed in the opposite group order. Both estimates describe a contrast of similar magnitude and both intervals include zero.

The recalculation is not a replacement for the sponsor’s analysis. It uses the posted summary statistics and is unadjusted; it cannot reproduce participant-level modeling or any details not stated in the registry record. The record does not flag a discrepancy. Accordingly, the sponsor-reported analysis remains the principal account of the trial’s own analysis, while the recalculation offers a transparent comparison based on the group summaries.

The secondary sponsor analysis is also listed as a Satterthwaite corrected t-test, with a net mean difference of -0.04, a 95% confidence interval from -0.79 to 0.72, and p = 0.92. The unadjusted summary-based estimate is 0.0. Its contrast is also expressed in the reverse direction. The record does not provide additional model detail that would allow a more exact reconciliation between the sponsor analysis and the summary-based calculation.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and one secondary endpoint, but a complete statistical analysis plan is not reported in the registry record. In particular, it does not state whether the secondary outcome was part of a formal testing hierarchy, whether the type I error rate was adjusted across outcomes, or whether any subgroup or additional analyses were prespecified. Without that information, the secondary result is best interpreted as a separate posted comparison rather than as evidence protected by a stated multiplicity strategy.

Multiplicity matters in general when several hypotheses are tested: the more opportunities there are to observe a seemingly unusual result, the greater the chance that at least one result may appear notable by chance. Methods such as adjustment or a prespecified ordered testing procedure can control that risk, but the record does not say whether either was used. The primary outcome remains the principal endpoint described in the record, and the secondary result should be interpreted with the absence of multiplicity details in mind.

The outcome counts vary by endpoint, but a participant-flow description is not reported. Reasons for missing measurements, withdrawals, exclusions, and the timing of any missingness are not reported in the registry record. The approach to missing data, including any imputation or sensitivity analysis, is also not reported. The record does not identify whether the analyses used all randomized participants, participants with available outcome data, or another defined analysis population.

These omissions do not establish that the analysis was biased or that missing data altered the results. They mean that the potential effect of missingness cannot be evaluated from the registry record alone. In general, interpretation is strengthened when the analysis population and missing-data handling are explicit, because readers can assess whether participants remain comparable after randomization and whether assumptions about unavailable measurements are plausible.

The registry does not report interim analyses, stopping rules, or protocol amendments relevant to statistical testing. Their absence from the record should not be taken as evidence that they did or did not occur. The documented design and posted analyses are the available basis for statistical interpretation.

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: deep venous thrombosis (4.2%).

The serious adverse event figures list 1 event among 24 participants at risk in the eplerenone group and 0 among 26 participants at risk in the placebo group. These counts describe the registry’s serious-event reporting; they do not by themselves establish that treatment caused an event or that a difference between groups is reliable. The record lists deep venous thrombosis as a top serious-event term at 4.2%, without further event-level detail in the posted information.

The at-risk counts differ from the numbers in the primary outcome analysis. Safety and efficacy counts can reflect different reporting populations or availability, but the registry record does not explain the difference. It also does not provide the specific definitions, observation details, or individual circumstances needed to interpret the events beyond the posted categories and counts. Deaths are not reported in the registry record.

These figures are descriptive. A small number of reported serious events cannot establish a comparative safety profile, and the absence of a reported event in a group does not establish that no such risk exists. No medical conclusion should be drawn from these counts alone.

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

The posted primary results estimate the difference between eplerenone and placebo in a physiological endpoint measured at 16 weeks. The sponsor-reported confidence interval includes zero, and the unadjusted recalculation also has an interval that includes zero. The results therefore do not establish a clear between-group difference on the primary measure. They also do not establish equivalence, because the intervals remain compatible with effects in either direction.

The secondary result follows a similar overall pattern, with no clear separation in the posted group summaries. Since the secondary endpoint is a distinct measure and multiplicity details are not reported, it should not be treated as an independent confirmation of the primary finding. The outcome counts, missing-data approach, and analysis populations are not fully explained, which adds uncertainty to interpretation.

The endpoint is a measure of coronary vascular response, not a direct measure of chest-pain relief, quality of life, or clinical events. Although the study rationale mentions possible symptom improvement, the posted results described in the registry do not establish whether symptoms changed. Nor do the 16-week physiological measurements answer questions about longer-term outcomes. Those outcomes are not reported in the registry record.

In general, a randomized comparison is designed to assess differences between assigned groups, but the strength of inference also depends on the conduct of the trial, outcome completeness, analysis choices, and precision. The registry identifies the broad design and reports group results, yet does not provide enough detail on participant flow, missing data, or the full statistical plan to resolve those issues. The appropriate conclusion is limited to the posted outcome estimates and their uncertainty, rather than a broader claim about clinical benefit or lack of benefit.

The results are not a treatment recommendation. They are a registry-level account of one study’s reported outcomes. The sample-size illustrations do not alter the observed findings, and they are not evidence that the trial did or did not have adequate power after completion.

18. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation should begin with the endpoint and its uncertainty, rather than with a p-value alone. The primary outcome estimate is accompanied by a confidence interval that includes zero and covers effects in either direction. That makes precision central: the result does not identify a single clear direction or tightly determine the size of a group difference.

It also illustrates the importance of contrast orientation. The sponsor’s estimate and the summary-based recalculation have opposite signs because the group order is reversed. Reading the comparison requires checking which group is subtracted from which, and then considering the interval and group means. Sign alone can be misleading when estimates are presented under different conventions.

The record offers an example of how outcome-specific counts matter. The primary and secondary analyses include different numbers of participants, and the reasons are not reported. Without participant flow and missing-data details, readers cannot fully assess how the analyzed groups relate to the randomized population. This does not invalidate the posted statistics, but it limits the conclusions that can be drawn from them.

Finally, the original design description and the observed-effect planning illustrations answer different questions. The former records planned assumptions; the latter explores sample sizes under stated hypothetical planning assumptions based on the observed effect. Keeping these distinct prevents planning calculations from being mistaken for a retrospective measure of success. The study is therefore useful for teaching how estimates, intervals, analysis populations, outcome hierarchy, and design assumptions all contribute to a cautious reading of clinical trial results.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not include a detailed participant-flow account. Although enrollment was 70, the outcome-specific analysis counts are smaller, and the reasons are not reported. Withdrawals, exclusions, missing measurements, and the treatment of missing data are not described. This prevents assessment of whether the analyzed participants represent the randomized groups adequately.

The full statistical analysis plan is not reported. The record identifies the sponsor’s test and describes baseline adjustment for the primary endpoint, but does not provide the full model specification, analysis population, or details of any sensitivity analyses. The relation between the baseline-adjusted endpoint description and the reported test is not explained in enough detail to reproduce the sponsor’s analysis from the registry record.

The record does not state whether multiplicity was addressed, whether outcomes were ordered in a testing hierarchy, or whether interim analyses or relevant protocol changes occurred. It also does not report a threshold for a clinically important difference. Consequently, statistical uncertainty cannot be translated into a judgment about the clinical importance of the observed estimate, and the secondary result should be interpreted cautiously.

The study reports physiological outcomes at 16 weeks. The registry does not report a direct chest-pain outcome among the posted results described, nor does it provide longer-term outcome results. The safety information is limited to the posted serious-event counts and a listed event term; deaths and fuller event details are not reported in the registry record.

These limitations concern what can be concluded from the registry record. They do not establish that unreported procedures were absent or that the findings are invalid. They define the boundaries of what can be assessed from the available study description and posted results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: EWISE: Study of Eplerenone in Women With Chest Pain, Coronary Vascular Dysfunction and Evidence of Myocardial Ischemia — NCT00187889.
• Registry record last updated 2013-10-14; status last verified 2011-10.
• Results first posted 2013-10-14.
• 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

EWISE is a completed, phase 4, randomized, double-blind, parallel-group, placebo-controlled study sponsored by the University of Florida. It enrolled 70 women described as having chest pain, coronary vascular dysfunction, and evidence of myocardial ischemia without significant epicardial coronary artery disease. Eplerenone was compared with placebo over a 16-week treatment period.

The primary endpoint measured baseline-adjusted change in epicardial coronary artery response to acetylcholine at 16 weeks. The sponsor-reported primary comparison and the unadjusted summary-based recalculation both have confidence intervals that include zero. The posted secondary measure of microvascular coronary flow reserve shows no clear separation in the group summaries.

Interpretation is constrained by unreported participant flow, missing-data procedures, analysis-population definitions, multiplicity handling, and full model details. The registry results describe vascular-function outcomes and do not establish effects on chest pain or longer-term outcomes.