Dietary Nitrate and Physiological Aging: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dietary Nitrate and Physiological Aging (NCT02593305), a randomized na study. The primary outcome is Change in Carotid Chemosensitivity Following 4 Weeks of Dietary Nitrate Supplementation and Placebo in Older Adults.

2. Clinical Question

The study also aimed to examine peripheral chemoreceptor sensitivity, spontaneous baroreflex sensitivity, blood pressure responsiveness to physiological stressors, central artery stiffness, and aortic blood pressure. These aims describe the broader study purpose, not additional outcome results available in the posted record. The registry lists 2 outcome measures, but no secondary results are posted. The primary outcome is therefore best read as a focused physiological measure in the older participants, rather than as a complete account of every aim or measure in the study.

3. Trial Design

The registry identifies NCT02593305 as a completed, randomized, double-masked crossover study, with an enrollment of 23 and a start date of 2015-10. Primary completion was 2017-04-28. The listed phase is NA. The sponsor is Darren P Casey, and Aging is the listed condition.

Older participants were assigned to one of two sequences. In one sequence, they received nitrate-rich beetroot powder for 4 weeks, had a 4 weeks washout, and then received placebo for 4 weeks. In the other, the order was placebo followed by nitrate, again separated by a 4 week washout. The registry describes nitrate-rich powder at 10g/day and placebo as beetroot powder without nitrate. A separate young comparison group was used for age-related comparisons and did not go through an intervention.

A crossover design means that participants receive more than one intervention period, so each participant can contribute measurements under both conditions. The order and washout are relevant when interpreting a crossover study, because period, sequence, or carryover effects can affect comparisons. Whether the study analyzed or adjusted for these features is not reported in the registry record.

The outcome summaries give 13 observations for each of Nitrate Pre, Nitrate Post, Placebo Pre, and Placebo Post. These are measurements at different times and conditions, not four independent groups of participants. The young comparison group is not included in these primary outcome summaries. Although the registry marks the study completed, it does not report how many participants completed each period or how missing outcome observations were handled.

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.

Baseline 1

Post 1

Reasons for not completing this period:

Baseline 2

Post 2

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 Change in Carotid Chemosensitivity Following 4 Weeks of Dietary Nitrate Supplementation and Placebo in Older Adults, measured over Pre and post 4 weeks dietary nitrate supplementation and pre and post 4 weeks of placebo..

The primary endpoint is change in carotid chemosensitivity following 4 weeks of dietary nitrate supplementation and placebo in older adults. The registry describes carotid chemosensitivity as hypoxia ventilatory responsiveness. It was quantified through the change in ventilation in relation to the change in pulse oxygen saturation, with units of L/min/%SpO2. Measurements were scheduled before and after each 4-week period.

This endpoint is used as a physiological measure of the ventilatory response associated with hypoxia and carotid chemoreflex sensitivity. In general, expressing the measure as ventilation change in relation to oxygen-saturation change characterizes the response across those two quantities, rather than reporting ventilation alone. This is a description of the measurement concept, not evidence that a change is beneficial or clinically important.

The registry lists the outcome parameter as a mean and its dispersion as standard error. The posted values are therefore group means accompanied by standard errors. The registry does not give a threshold for a meaningful change, nor does it report an established clinical interpretation for the size or direction of the endpoint values. The other physiological outcomes mentioned in the study purpose do not have secondary results posted in the record.

7. Results Posted in the Registry

• Nitrate Pre: mean -0.13 versus -0.10 on control; difference -0.03 (95% CI -0.16 to 0.10), standardized effect d = -0.18; z-test p = 0.639.
• Nitrate Post: mean -0.05 versus -0.10 on control; difference 0.05 (95% CI -0.06 to 0.16), standardized effect d = 0.36; z-test p = 0.353.
• Placebo Post: mean -0.11 versus -0.10 on control; difference -0.01 (95% CI -0.15 to 0.13), standardized effect d = -0.06; z-test p = 0.888.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a mean describe?

A mean is a measure of the center of a set of continuous observations. Here the outcome is a physiological response expressed in L/min/%SpO2. A mean condenses the observations into a single value, but does not show the full spread or shape of the individual measurements. Two conditions can have similar means while differing in the distribution of participant-level values.

The registry reports standard errors alongside the means. In general, a standard error describes the precision of an estimated mean: smaller standard errors indicate that the mean is estimated more precisely, while larger standard errors indicate greater uncertainty. A standard error is not the same as the spread of individual values. The registry does not post standard deviations for the four endpoint summaries.

What do the recalculated differences represent?

The registry record contains no posted analyses. The displayed mean differences, confidence intervals, and unadjusted p-values are simple recalculations from the posted summary statistics. For these comparisons, each of Nitrate Pre, Nitrate Post, and Placebo Post is compared with Placebo Pre. These are unadjusted contrasts between summary means; they are not a participant-level crossover model and do not directly compare the change during nitrate with the change during placebo.

In general, a mean difference expresses the separation between two means in the units of the original outcome. A positive estimate indicates that the first mean in the stated contrast is numerically higher than the reference mean; a negative estimate indicates it is numerically lower. The sign alone does not establish clinical importance or a favorable outcome. Interpretation also depends on how the endpoint is defined and on the uncertainty around the estimate.

How should confidence intervals and p-values be read?

In general, a confidence interval describes a range of values compatible with the data and the method used to calculate it. Wider intervals indicate less precision. The recalculated intervals for all three contrasts include zero, so the range of values includes no difference. Each also allows differences in either direction. An interval that includes zero does not prove equality or rule out a meaningful difference.

A p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the test. The recalculated p-values are unadjusted. They are not the probability that the null hypothesis is true, and they do not measure the size or practical importance of a difference. Because the record does not post the sponsor’s tests or statistical analysis plan, these recalculated values should not be presented as the trial’s reported inferential analysis.

Why is the crossover structure important?

In general, crossover designs compare conditions within the same participants. A suitable analysis can account for that pairing, which often affects the uncertainty of a within-person contrast. The outcome summaries give 13 observations at each of four time-condition combinations, but they do not give the participant-level paired values or the correlation between repeated measurements. Those details are needed to reconstruct a paired analysis from the summaries.

Period and sequence can also matter in a crossover trial. A period effect is a change associated with when a measurement was taken, apart from the intervention itself. A sequence effect concerns the order in which participants received the conditions. Carryover refers to an effect of one period persisting into a later period. The registry describes a 4 weeks washout but does not report whether these issues were assessed, what model was used, or whether any adjustment was made. It is not possible to infer the original analytic choices from the sequence description alone.

What does over-dispersion mean in general?

Over-dispersion arises when variability in the data is greater than a statistical model expects. It is especially discussed for count outcomes, where extra variability can make model-based uncertainty too small if not accommodated. The primary endpoint is continuous, and the record does not report an over-dispersion assessment or a model for the primary outcome. This general concept does not identify a problem in this trial; it explains why model assumptions should be considered when interpreting statistical uncertainty.

What information is missing about the analysis?

The registry record does not report the original statistical plan, the sample-size justification, interim analyses, the handling of missing data, or the analysis population. It also does not describe the model used for the primary endpoint, any adjustment for sequence or period, or the approach to repeated measurements. The record lists 2 outcome measures but has no posted secondary results. Without those details, the recalculations can offer a transparent but limited reading of the posted means; they cannot establish what the investigators planned or how they analyzed participant-level data.

10. Confidence Intervals and Precision

The group means are reported with standard errors: Nitrate Pre is -0.13 (standard error 0.04), Nitrate Post is -0.05 (0.02), Placebo Pre is -0.1 (0.05), and Placebo Post is -0.11 (0.05). Each summary has 13 observations. These standard errors indicate uncertainty in the mean estimates, not the range of individual responses. The registry does not post confidence intervals for the four means.

The recalculated unadjusted mean differences have confidence intervals that all include zero. This is a central point for reading precision: the estimates do not pin down a single effect, and values on both sides of zero remain compatible with the summaries. The intervals are broad enough that the data do not precisely determine the direction or magnitude of these unadjusted contrasts. Exact interval bounds are not needed to see that the uncertainty includes no difference.

Confidence intervals are not guarantees that the true value lies within a particular interval. In general, they describe the range generated by a specified method under its assumptions. These particular intervals come from simple unadjusted recalculations, rather than a posted sponsor analysis. They do not account for the within-participant pairing or the full crossover structure, because the necessary participant-level information and analysis details are not reported in the registry record.

Precision is distinct from statistical significance and clinical importance. An interval spanning zero does not establish equivalence, and an estimate’s location does not by itself show whether a difference matters clinically. The registry record does not state a meaningful-change threshold. The small outcome summaries and absent paired-data details limit how much can be concluded about the precision of a crossover treatment contrast.

11. 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 illustrations calculated from an observed effect, not the trial’s original design calculation. The listed assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning target uses a stated fraction of an observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the selected effect under the stated assumptions, if that effect and assumptions were correct. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are planning concepts, not guarantees that a future study will detect an effect.

Rows labeled planning for 100% of the observed effect use the full observed estimate; rows planning for 75% or 50% use smaller target effects. Smaller effects need more participants to detect, so the required sample sizes rise as the target effect shrinks. For example, planning for 75% of the observed Nitrate Post contrast gives 211 participants per arm for 80% power and 282 participants per arm for 90% power. The other contrasts produce different illustrations because their observed estimates differ.

The trial’s crossover structure and small outcome summaries matter when interpreting these calculations: the planning assumptions describe a two-arm equal-allocation approximation, not a reconstructed crossover design analysis. These figures are not observed power.

12. 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 = -0.030; pooled standard deviation σ = 0.163.
2. n = 2 × (1.96 + 0.842)² × 0.163² / -0.030² = 464.8, rounded up to 465 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 <- -0.03                      # observed difference in means
sigma <- 0.163248277173145                     # 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(2593305)
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 = 465 (80% power), 623 (90% power)
 75% of observed effect: n per arm = 827 (80% power), 1,107 (90% power)
 50% of observed effect: n per arm = 1,860 (80% power), 2,490 (90% power)
power.t.test: 465.8 
Simulated power at n = 465 per arm: 0.796 (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.

13. Multiplicity, Missing Data and Analysis Populations

The study description names several physiological aims, including chemoreceptor sensitivity, baroreflex sensitivity, blood pressure responsiveness to stressors, central artery stiffness, and aortic blood pressure. The registry lists 2 outcome measures, but no secondary results are posted. The record does not explain how many statistical comparisons were planned for these aims or whether any adjustment for multiple comparisons was intended.

In general, testing multiple outcomes or contrasts can increase the chance of observing a nominally unusual result by chance. Methods for addressing multiplicity depend on the questions and analysis plan. No multiplicity procedure is reported in the registry record, so the unadjusted recalculated p-values should not be read as adjusted evidence across the study’s full set of aims.

The record also does not report how missing data were handled, whether all randomized participants were included in the primary analysis, or the definition of the analysis population. Although the registry marks the study completed and gives an enrollment of 23, the number completing each treatment period and the number included in each primary outcome summary beyond the reported 13 observations are not described. The summaries alone cannot show whether observations were missing or excluded, or why.

For a crossover analysis, participant-level pairing, period, sequence, and possible carryover can affect the estimated contrast and its uncertainty. The registry describes randomized order and a 4 weeks washout, but does not report the analysis model or whether those design features were incorporated. Interim analyses and the original statistical plan are also not reported in the registry record. These omissions limit assessment of multiplicity, missing-data bias, and whether the recalculated contrasts correspond to the analysis intended by the investigators.

14. 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 serious adverse event summaries report 0 affected participants among 13 at risk in the Nitrate group and 0 among 13 at risk in the Placebo group. The Young Comparison Group reports 0 affected among 10 at risk. Deaths are listed as 0 in each group. The record also lists 0 participants affected by other adverse events in each of these groups, among the same numbers at risk. No serious adverse event terms are listed.

These figures describe what is recorded for the groups and the risk counts shown; they do not establish that an intervention has no risk. With no affected participants recorded in these relatively small groups, the registry summary cannot precisely characterize uncommon events. The young comparison group did not receive an intervention, so its figures are not a treatment comparison. The registry record does not provide further detail about event collection, duration of safety follow-up, or how adverse events were defined.

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

The posted outcome means describe carotid chemosensitivity measurements before and after the nitrate and placebo periods in older adults. The simple recalculated contrasts compare Nitrate Pre, Nitrate Post, and Placebo Post separately with Placebo Pre. Their estimates are -0.03, 0.05, and -0.01, respectively, and their unadjusted p-values are 0.639, 0.353, and 0.888. Each recalculated confidence interval includes zero.

These statistics do not establish that nitrate and placebo produced the same change. The comparisons are not a direct within-participant contrast between the change in the nitrate period and the change in the placebo period. They also do not establish that either condition changed chemosensitivity, because the registry does not post a paired crossover analysis. The original statistical model and analysis plan are not reported in the registry record.

The results do not show whether any difference is clinically important. The record does not give a threshold for meaningful change or a clinical interpretation of the endpoint’s magnitude. A p-value above a conventional threshold is not proof of no effect, and intervals that include zero do not demonstrate equivalence. The available summaries are compatible with uncertainty in both the size and direction of the unadjusted differences.

The endpoint is a physiological measure of hypoxia ventilatory responsiveness, not a direct measure of patient-centered outcomes. The wider study aims include other physiological measures, but no secondary results are posted. These data therefore do not answer every question raised by the study description. They provide a limited statistical description of the primary outcome summaries and should not be turned into medical advice or a broad claim about treatment effects.

16. Why This Trial Matters Statistically

This trial is statistically interesting because it uses a randomized crossover design for a continuous physiological outcome. In general, crossover designs can make within-person comparisons useful by observing participants under more than one condition. To make that advantage interpretable, however, the analysis needs to account for the paired measurements and for the timing and order of treatment periods. The registry gives the sequences and washout but does not report how the analysis handled those features.

The difference between the design and the available recalculations is important. The posted means allow simple unadjusted comparisons, but these are not the same as a crossover treatment-effect estimate. Without participant-level paired data or the sponsor’s model, the recalculations cannot use the within-person relationship that defines the design. This is a practical example of why a trial’s design should guide statistical interpretation, rather than treating each summary as though it came from a separate independent group.

The case also illustrates the role of precision. The group summaries are based on 13 observations, and the recalculated confidence intervals include zero while leaving uncertainty about effect size and direction. A non-small p-value alone does not resolve that uncertainty. Planning illustrations likewise depend on the chosen target effect and assumptions; they are not evidence of the probability that the completed study detected an effect.

Finally, the registry record distinguishes an extensive set of study aims from the smaller set of posted results. Clear reporting of the analysis model, paired-data handling, missing observations, and multiplicity strategy would help readers evaluate how the primary result was obtained. The available information still permits a careful account of the means and their limits, while underscoring why incomplete analysis details matter in clinical statistics.

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 primary outcome summaries contain 13 observations at each of four measurement labels, but the registry does not provide participant-level values or identify the paired observations. This prevents reconstruction of a within-person nitrate-versus-placebo change estimate. The simple recalculations use summary means and standard errors and should not be mistaken for a crossover model.

The registry record does not report whether the results account for treatment sequence, period, or carryover, despite the described 4 weeks washout. It also does not state the original statistical plan, model, missing-data method, or analysis population. Completion status and total enrollment do not establish how many participants contributed complete data to every period or outcome.

The primary endpoint description refers to beetroot juice, while the intervention and arm descriptions refer to beetroot powder or crystals. The record does not explain this terminology difference. It also does not provide a clinical threshold for meaningful change, nor does it post secondary outcome results despite describing broader physiological aims.

The sample-size illustrations are based on observed effects under a two-arm normal approximation, while this study is a crossover trial. They are therefore not a report of the original design rationale. The young comparison group did not receive either intervention and is not part of the primary outcome summaries, so it cannot serve as a randomized treatment comparator. These limitations constrain interpretation to the posted physiological summaries and simple recalculations.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Dietary Nitrate and Physiological Aging — NCT02593305.
• Registry record last updated 2019-10-14; status last verified 2019-09.
• Results first posted 2019-10-14.
• 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.

21. Record Summary

NCT02593305 is a completed randomized, double-masked crossover study titled Dietary Nitrate and Physiological Aging. The registry lists an enrollment of 23, a start date of 2015-10, and primary completion on 2017-04-28. Older participants received nitrate-rich beetroot powder and placebo in alternating order, separated by a 4 weeks washout; a young comparison group received no intervention.

The primary endpoint was carotid chemosensitivity measured as hypoxia ventilatory responsiveness before and after each 4-week period. The four posted summaries each contain 13 observations. The registry record has no posted analyses or secondary results. Simple unadjusted recalculations compare three summary means with Placebo Pre, but do not constitute a participant-level crossover analysis. The recalculated intervals include zero, and the record does not report the original statistical plan, missing-data approach, or clinical threshold for interpreting a change.