The Role of Aldosterone on Augmented Exercise Pressor Reflex in Hypertension: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Role of Aldosterone on Augmented Exercise Pressor Reflex in Hypertension (NCT01996449), a randomized phase 2 study. The primary outcome is Muscle Sympathetic Nerve Activity at Rest.

2. Clinical Question

The clinical rationale in the registry is that hypertension may be accompanied by an exaggerated blood-pressure response during exercise, attributed to overactivity of the exercise pressor reflex. The study hypothesis is that aldosterone contributes to this reflex through a direct action on the central nervous system, and that mineralocorticoid receptor antagonists could affect reflex overactivity independently of changes in resting blood pressure. These are the rationale and hypothesis recorded for the study, not conclusions established by the posted outcome summaries.

In statistical terms, the primary comparison is between average resting nerve activity under two treatment conditions. The trial also measured activity during exercise, giving a related outcome for considering whether any pattern at rest is also present during exertion. The registry does not post a detailed protocol explaining how the measurements were timed or how each participant’s paired treatment observations were analyzed.

3. Trial Design

The registry identifies this as a phase 2, randomized, single-masked, crossover study sponsored by the University of Texas Southwestern Medical Center. Enrollment was 14. The study started in 2013-07, reached primary completion in 2021-04, and is listed as completed. These dates describe the registry record and do not explain the duration of recruitment or any pauses in the study.

The two treatment conditions were amlodipine and eplerenone. Descriptions of the arms say that participants began one of the medications, continued it for a 12-week period, and then underwent study procedures. They also state that the medication would be discontinued after the procedures. Because the design is identified as crossover, treatment conditions are intended to be compared within a study structured around more than one treatment condition. The precise order, sequence allocation, washout arrangements, and procedures for switching treatments are not reported in the registry record.

The outcome timeframe is given as 8 weeks post treatment initiation for both the primary and secondary outcomes. The arm descriptions refer to study procedures following a 12-week treatment period. The registry does not explain the relationship between these timing statements, so the exact measurement schedule cannot be resolved from the record alone.

The primary outcome was muscle sympathetic nerve activity at rest, in bursts per minute, measured by microneurography using intraneural microelectrodes. The secondary outcome was muscle sympathetic nerve activity during exercise, also in bursts per minute. The record lists additional procedures, including handgrip and arm-cycling exercise, forearm blood flow assessment, and a cold pressor test, but it does not post separate results for each procedure.

Fourteen observations are listed for each treatment condition. The registry does not report a participant flow account, the number completing each period, or how missing measurements were handled. It also does not identify which party or parties were masked.

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.

Period 1: First Drug

Period 2: Second Drug

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 Muscle Sympathetic Nerve Activity at Rest, measured over 8 weeks post treatment initiation.

The primary endpoint is muscle sympathetic nerve activity at rest, reported as a mean in bursts per minute with a standard deviation for each treatment condition. Microneurography uses intraneural microelectrodes to measure sympathetic nerve activity. This provides a physiological measure related to the study’s question about sympathetic nervous system activity in hypertension and the proposed role of aldosterone.

A resting measurement is useful for assessing nerve activity outside the exercise challenge. It is distinct from the exercise endpoint, which captures activity during exertion and may reflect responses to the exercise pressor reflex. Considering both can describe whether the observed treatment-condition pattern is limited to rest or also appears during exercise. Neither measure by itself establishes the mechanism proposed in the study rationale.

The posted primary summaries are means and standard deviations. A mean describes the average observed activity in a treatment condition; a standard deviation describes the spread of individual measurements around that average. The comparison is expressed as a mean difference for eplerenone relative to amlodipine. Its interval communicates uncertainty around that estimated difference. The registry does not give participant-level values, a distribution plot, or a detailed account of the model used to estimate the comparison.

The outcome timeframe is stated as 8 weeks post treatment initiation, while the treatment descriptions refer to procedures after a 12-week period. The record does not reconcile these descriptions. This ambiguity matters when interpreting precisely when the primary measurement was taken.

7. Results Posted in the Registry

• Eplerenone: mean 43.80 versus 41.00 on control; difference 2.80 (95% CI -6.36 to 11.96), standardized effect d = 0.23; z-test p = 0.549.

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.

Muscle Sympathetic Nerve Activity During Exercise

• 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 51.00 versus 47.00 on control; difference 4.00 (95% CI -8.62 to 16.62), standardized effect d = 0.23; z-test p = 0.534.
• 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 secondary endpoint, muscle sympathetic nerve activity during exercise, has the same broad descriptive direction as the primary endpoint: the posted mean is higher in the eplerenone condition than in the amlodipine condition. Its interval also includes zero. This pattern is broadly consistent with the primary result in that neither posted comparison precisely distinguishes the treatment conditions, but the secondary endpoint does not independently settle the primary question.

The exercise measure is related to the study rationale because the registry discusses the exercise pressor reflex and lists exercise procedures. It complements the resting measurement by describing nerve activity during exertion. However, a shared direction across two outcomes does not establish that the effects are the same, that the endpoints measure the same process, or that the proposed mechanism is confirmed. No formal comparison between resting and exercise responses is reported.

The record lists one secondary outcome but no reported analyses. The posted descriptive summaries and comparison do not include a detailed secondary analysis plan, adjustment for multiple testing, or explanation of how the crossover structure was used. Because secondary outcomes are typically interpreted in the context of the primary analysis and the study’s prespecified hierarchy, lack of those details gives the secondary evidence less weight.

Unadjusted secondary findings can be more vulnerable to chance patterns when multiple outcomes or analyses are considered. This is a general statistical concern, not evidence that any particular finding in this trial is a false positive. The registry does not report the full set of planned or conducted analyses, so the extent of multiplicity cannot be determined. The exercise results are best treated as descriptive context rather than a separate confirmatory conclusion.

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

• Muscle Sympathetic Nerve Activity During Exercise

9. Statistical Interpretation

10. Statistical Methods Explained

The registry posts continuous outcomes as means and standard deviations. These are descriptive summaries: the mean is the average measurement, while the standard deviation describes variation among measurements. The comparison is reported as a mean difference between eplerenone and amlodipine. The sign indicates the direction of the estimate according to that ordering; it does not by itself determine whether the difference is important.

What does the interval communicate?

A confidence interval is a range of estimates compatible with the observed data under the assumptions of the analysis. It conveys precision as well as direction. A narrower interval indicates more precision than a wider interval, while an interval spanning zero leaves open the possibility of no average difference. The registry gives interval limits but does not specify the confidence level in the outcome record, so no confidence level should be inferred from the displayed limits.

For the primary comparison, the estimated mean difference is 2.8, with limits -6.362 and 11.96. Since the limits extend on both sides of zero, the estimate does not narrowly pin down the direction or size of the difference. An interval is not a range containing every participant’s measurement, and it does not mean that all values within it are equally likely. It concerns uncertainty in the estimated contrast.

How should a p-value be read?

A p-value measures how unusual the observed data, or data more extreme, would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is correct, and it does not measure the probability that a result occurred by chance. The primary comparison has an unadjusted p-value of 0.549. The registry does not post the full model specification or a prespecified decision threshold for the primary analysis. The p-value therefore needs to be read alongside the estimate, interval, design, and reporting limitations.

“Unadjusted” means the posted p-value has not been adjusted for a family of multiple comparisons. Multiple testing can increase the chance of at least one apparently notable result when many outcomes or contrasts are examined. The registry lists a primary and a secondary outcome, but does not report a multiplicity procedure. That absence limits how strongly secondary p-values, if available, could be interpreted; the record does not post reported secondary analyses.

Why does the crossover design matter?

In a crossover design, the same participant can contribute measurements under different treatment conditions. Such observations are related, rather than independent. An analysis can account for this pairing and can also consider period or sequence effects, depending on the design and protocol. If the comparison is analyzed as though treatment groups were independent, that may not reflect the information structure of a crossover study. The registry does not report whether the posted comparison uses paired data, how period or sequence was handled, or whether any carryover assessment was performed. It is therefore not possible to assess those details from the registry summary.

There are 14 observations listed under each treatment condition, while total enrollment is 14. This is consistent with both conditions contributing summaries for the enrolled sample, but the record does not give participant-level completion or missingness details. Equal counts do not reveal whether every participant contributed both measurements or how incomplete pairs, if any, were treated.

Why can over-dispersion matter?

General statistical explanation: over-dispersion occurs when the observed variability is greater than a model assumes. It can make standard errors too small and intervals too narrow if the analysis does not allow for the extra variation. This concern is most relevant to outcomes whose variance structure is modeled, including counts; the registry’s posted outcomes are continuous measurements summarized by means and standard deviations. The record does not report a model diagnostic or a formal assessment of dispersion, so no claim about over-dispersion in this trial can be made.

What do the standard deviations add?

The standard deviation describes spread within each treatment-condition summary, not uncertainty in the mean difference. Standard deviations of 11.7 and 13.0 are posted for resting activity under amlodipine and eplerenone, respectively. The comparison interval incorporates uncertainty in the contrast, although the registry does not explain its exact calculation. In a crossover study, the variability of within-participant differences can be especially relevant, and that quantity is not reported.

The record contains no reported analyses for the secondary outcome and no detailed statistical analysis plan. The original sample-size assumptions, any interim analyses, the prespecified treatment of missing data, and analysis populations are not reported in the registry record. These omissions do not invalidate the descriptive statistics, but they restrict what can be established about confirmatory inference and the analysis’s alignment with the intended design.

11. Confidence Intervals and Precision

The primary comparison estimates a mean difference of 2.8 bursts per minute, with an interval from -6.362 to 11.96. The interval spans zero and covers effects in both directions. It therefore does not identify a clear direction with high precision, and it leaves substantial uncertainty about the size of the contrast. The point estimate should not be interpreted in isolation from that range.

Confidence intervals are useful because they show the uncertainty that a single estimate conceals. A narrow interval can support a more precise statement about the size of a contrast; a broad interval leaves more plausible values open. Here, the posted limits permit interpretations ranging from lower activity with eplerenone to higher activity. The record does not state a confidence level, so the interval should be described by its posted limits rather than assigned an assumed level.

The sample contributing to each treatment summary is 14. Small samples generally provide less information for estimating a mean difference than larger samples, all else equal. In a crossover study, the precision may also depend on how strongly measurements from the same participant are related. The registry does not provide the variability of paired differences, so the contribution of within-person pairing to precision cannot be assessed from the summaries.

No clinically important difference threshold is reported. Thus, the interval cannot be classified as excluding or including effects that would be clinically meaningful. Nor does it establish equivalence: that requires a prespecified margin and an analysis designed to assess whether the interval lies within that margin. The posted result is best read as an uncertain estimate rather than a definitive statement that the treatment conditions do or do not differ.

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 figures are participants per arm, not total events. They are illustrative calculations based on the observed effect, not the trial’s own original design assumptions. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each planning scenario targets the stated fraction of the observed effect. The original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for a hypothetical study to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the calculation assumptions were correct. The 90% power column uses a higher target chance of detection and therefore calls for more participants per arm under the same scenario. These are planning quantities, not guarantees about the result of a future study.

The entries consider planning for 100%, 75%, and 50% of the observed effect. A smaller target effect is harder to distinguish from random variation, so more participants are needed. The figures are especially sensitive to the observed effect used as the starting point: estimates from a small study can be uncertain, and planning directly from them may produce unstable projections.

This is not observed power. It does not describe the probability that the completed trial detected an effect, and it cannot repair the limited precision of the posted estimate. The registry identifies a crossover design, while these illustrations state equal allocation between two arms and do not describe a paired-data calculation. The record does not report whether these planning calculations reflect the trial’s crossover structure, so they should be read only according to their stated illustration assumptions.

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 = 2.800; pooled standard deviation σ = 12.367.
2. n = 2 × (1.96 + 0.842)² × 12.367² / 2.800² = 306.2, rounded up to 307 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 <- 2.8                      # observed difference in means
sigma <- 12.3670934337863                     # 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(1996449)
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 = 307 (80% power), 410 (90% power)
 75% of observed effect: n per arm = 545 (80% power), 729 (90% power)
 50% of observed effect: n per arm = 1,225 (80% power), 1,640 (90% power)
power.t.test: 307.2 
Simulated power at n = 307 per arm: 0.803 (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. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary outcome and a secondary outcome, but does not report a multiplicity adjustment or a formal hierarchy governing interpretation of multiple outcomes. The primary comparison is accompanied by an unadjusted p-value. The secondary outcome has no reported analyses. Without a stated plan, it is not possible to determine whether the posted comparisons were the only planned tests or how any additional analyses were intended to affect interpretation.

Multiplicity matters because the chance of seeing an apparently unusual result can increase when many hypotheses are tested. Adjustment procedures or a prespecified hierarchy can address that issue, but the choice depends on the intended analysis. No adjustment method is reported in the registry record. The secondary summaries should therefore be interpreted as supporting description rather than as independent confirmatory evidence.

Missing-data methods and analysis populations are also not reported in the registry record. The record lists 14 observations for each treatment condition and total enrollment of 14, but does not state whether all participants completed both conditions, whether any measurements were missing, or how incomplete crossover pairs were handled. It does not define an intention-to-treat, per-protocol, or other analysis population.

These details are particularly relevant to a crossover design, where a participant may contribute observations under multiple conditions. Excluding participants with an incomplete sequence or analyzing only complete pairs can affect both the sample represented and the precision of the contrast. The registry does not say whether either situation occurred. No missingness pattern, imputation method, or sensitivity analysis is reported.

The record also does not report interim analyses or stopping rules. Their absence from the record should not be interpreted as evidence that they were or were not part of the original plan. Taken together, the missing analysis details limit assessment of prespecification, control of false-positive risk, and the extent to which the posted comparisons reflect the full randomized sample.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry lists zero serious adverse events in the amlodipine condition and zero in the eplerenone condition. It also lists zero other adverse events in each condition and zero deaths. Fourteen participants are listed as at risk for each adverse-event category under each treatment condition.

These counts describe the events recorded in the registry. They do not establish that no adverse events occurred beyond those captured or reported, and they do not show that the treatments have identical safety profiles. With 14 listed at risk per condition, the record offers limited information about uncommon events. The adverse-event summary does not provide event descriptions, severity details for non-serious events, timing, or an account of how events were collected.

The registry lists no serious adverse-event terms. This should be read as no serious events posted for these groups, rather than as proof that serious events are impossible. The crossover design also means the same participants may contribute to both treatment-condition summaries; the record does not explain whether the at-risk counts represent unique people per condition or how exposure periods were handled. Safety interpretation is therefore limited to the posted counts and reporting detail.

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

The results show that the posted average resting muscle sympathetic nerve activity was 41.0 bursts per minute with amlodipine and 43.8 with eplerenone. The estimated contrast is 2.8 bursts per minute for eplerenone relative to amlodipine, and the interval from -6.362 to 11.96 includes zero. The exercise outcome has a similar broad pattern of a higher posted mean with eplerenone and an interval including zero. These summaries describe the recorded measurements; they do not establish a treatment effect or the absence of one.

The primary interval is compatible with more than one direction and a range of possible sizes. The p-value does not demonstrate equivalence, and no equivalence margin is reported. The study also does not post a clinically important difference threshold, so statistical uncertainty cannot be translated into a judgment about clinical importance.

The registry’s scientific rationale proposes that aldosterone may augment the exercise pressor reflex through a central nervous system action and suggests a possible role for mineralocorticoid receptor antagonism. The posted endpoint summaries do not directly test every link in that proposed pathway. No formal mediation result or analysis of the blood-pressure response is posted. A difference, or lack of a clearly resolved difference, in nerve activity alone would not prove or disprove the proposed mechanism.

The study is small and crossover, yet the registry does not report the paired analysis details, missing-data handling, or original statistical plan. Those omissions affect how confidently the comparison can be interpreted. The results should not be generalized beyond the population represented in this study, whose characteristics are not fully described in the registry record.

In short, the posted data offer descriptive estimates for resting and exercise nerve activity in the two treatment conditions. The primary comparison is imprecise, and its interval includes no difference as well as differences in either direction. The record does not establish clinical benefit, harm, equivalence, or a mechanism. Further conclusions would require information and analyses not reported in the registry record.

17. Why This Trial Matters Statistically

This study is statistically notable because it combines a small enrollment with a crossover design and physiological measurements relevant to a stated mechanistic hypothesis. Crossover designs can be efficient when within-person comparisons are appropriately analyzed, since each participant can serve as their own reference. That potential advantage depends on design and analysis details such as treatment sequence, period effects, carryover, and the handling of incomplete observations. Those details are not reported in the registry record.

The posted treatment-condition means are close in scale to the uncertainty represented by the primary interval, which spans zero and extends in both directions. This illustrates why a point estimate or p-value alone is not enough: the interval communicates that the data do not provide a precise estimate of the contrast. It also illustrates why a non-significant result should not be recast as evidence of equivalence.

The exercise measure offers a related view of the study question, but its status as a secondary outcome and the absence of reported secondary analyses limit its confirmatory weight. A coherent biological rationale can motivate a study, but interpretation still depends on transparent methods, prespecified analyses, and adequate precision.

The registry record leaves important statistical questions unanswered, including the original sample-size justification, analysis plan, and treatment of repeated measurements. These gaps make it difficult to evaluate whether the posted comparison fully reflects the crossover design. The trial is therefore useful as an example of why reporting design-specific methods and uncertainty is essential when interpreting small clinical studies.

18. 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.

Enrollment was 14, and the registry lists 14 observations for each treatment condition. The limited sample contributes to uncertainty, as reflected in the interval for the primary contrast. The registry does not report a sample-size justification, so it is not possible to know what effect the trial was originally designed to detect or how that target was selected.

Although the study is described as crossover, the record does not explain the treatment sequence, washout, paired analysis, or handling of period and carryover effects. The posted group summaries do not include the variability of within-participant differences. These omissions make it difficult to assess whether the reported comparison appropriately reflects the design.

The timing information is not fully aligned: the outcomes are labeled as occurring 8 weeks post treatment initiation, whereas the arm descriptions state that procedures followed a 12-week treatment period. The registry does not explain the timing relationship. Which parties were masked is also not reported.

Participant characteristics beyond hypertension are not reported in the record, limiting assessment of how well the enrolled sample represents a broader population. Participant flow, completion by treatment period, missing observations, analysis populations, and missing-data methods are also not reported. The registry does not provide a detailed statistical analysis plan, interim-analysis information, or a multiplicity strategy.

Finally, the posted results focus on muscle sympathetic nerve activity. The record does not post a formal analysis of blood-pressure response or evidence directly establishing the proposed mechanism. The adverse-event counts are limited in detail and sample size. These limitations constrain interpretation of precision, design implementation, safety reporting, and the extent to which the physiological results address the broader hypothesis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Role of Aldosterone on Augmented Exercise Pressor Reflex in Hypertension — NCT01996449.
• Registry record last updated 2022-03-18; status last verified 2022-02.
• Results first posted 2022-02-23.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01996449 is a completed phase 2 randomized, single-masked crossover study sponsored by the University of Texas Southwestern Medical Center. The registry lists enrollment of 14 and a comparison of amlodipine with eplerenone in participants with hypertension.

The primary outcome was resting muscle sympathetic nerve activity, measured by microneurography and reported as a mean in bursts per minute. The posted comparison estimates a mean difference of 2.8 for eplerenone relative to amlodipine, with an interval from -6.362 to 11.96 and an unadjusted p-value of 0.549. The interval includes zero and indicates uncertainty about the direction and size of the contrast.

Muscle sympathetic nerve activity during exercise is listed as a secondary outcome. The registry does not report detailed analyses, crossover-specific methods, missing-data handling, or the original sample-size justification. It lists zero serious adverse events, zero other adverse events, and zero deaths in both treatment conditions.