The Role of Substance P on Perception of Breathlessness During Resistive Load Breathing: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Role of Substance P on Perception of Breathlessness During Resistive Load Breathing (NCT01580423), a randomized na study. The primary outcome is Intensity of Breathlessness.

2. Clinical Question

The trial asked whether oral aprepitant was associated with lower reported breathlessness during resistive load breathing than inert powder in people with chronic obstructive pulmonary disease (COPD). Its rationale was that Substance P, released from sensory nerves, transmits pain information into the central nervous system, and pain and dyspnea share characteristics, including similar neurological pathways. The study hypothesis was that blocking Substance P activity with aprepitant would reduce breathlessness ratings compared with placebo.

Breathlessness was rated on a 100 mm Visual Analog Scale, anchored by “No Intensity” and “Greatest Intensity.” Ratings were obtained at 1 minute intervals during resistive load breathing in Period 1 and Period 2. The primary outcome compared the time-weighted averages of those ratings.

This is a question about reported symptom intensity under the study’s breathing task and treatment conditions. It is not, by itself, a question about broader daily symptoms, long-term outcomes, or the effect of treatment outside the study setting; those outcomes are not reported in the registry record.

3. Trial Design

The registry describes a randomized, quadruple-masked crossover trial. Participants were assigned to treatment sequences, with aprepitant and inert powder assessed across Period 1 and Period 2. In a crossover design, participants receive more than one treatment condition, so comparisons can potentially use information from within the same participant. The registry record does not report the treatment sequence details or explain how the analysis handled the crossover structure.

The record lists 16 participants enrolled and reports 16 observations for each treatment condition on the primary outcome. These figures should not be added to infer the number of distinct participants: the study is identified as a crossover trial. The record gives the study start as 2012-04, primary completion as 2013-03, and status as completed. The sponsor is Dartmouth-Hitchcock Medical Center.

The masking level is recorded as quadruple, but the registry record does not specify which roles were masked or how masking was maintained. It also does not report the randomization sequence, allocation concealment procedures, washout details, treatment duration, or criteria for entering the analysis.

The primary outcome was assessed during resistive load breathing at 1 minute intervals. The registry describes measurements in Period 1 on Day 3 or 4 and in Period 2 on Day 5, 6 or 7. The record does not explain whether these day ranges corresponded to different participant schedules or provide further timing details.

The trial also posted a secondary pain-intensity outcome from cold-water hand immersion. The record identifies no reported statistical analysis descriptions. Details about the original sample-size justification, planned interim analyses, prespecified statistical model, and analysis populations 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: 17 subjects recruited; 1 patient who signed the consent form did not meet inclusion/exclusion criteria, and no testing was performed.

First Intervention

Second Intervention

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 Intensity of Breathlessness, measured over At 1 minute intervals during Resistive Load Breathing at Period 1 (Day 3 or 4) and Period 2 (Day 5, 6 or 7).

The primary endpoint is the time-weighted average of participants’ intensity-of-breathlessness ratings during resistive load breathing. Participants rated intensity on a 100 mm Visual Analog Scale, with “No Intensity” at the bottom and “Greatest Intensity” at the top. Ratings were obtained at 1 minute intervals during the breathing task in Period 1 and Period 2.

A time-weighted average combines the repeated ratings across the assessment interval into a summary that reflects the ratings over time rather than relying on a single moment. This can be useful when a symptom is measured repeatedly during a task and may change while the task continues. The registry does not give the specific computation used to form the time-weighted average.

The endpoint measures perceived intensity, not an objective measure of lung function or a direct measure of Substance P activity. Its relevance to the study question comes from the stated hypothesis that blocking Substance P activity could affect the sensation of dyspnea. The registry record does not report other primary outcomes or a separate threshold for a clinically important change.

The posted outcome is expressed in units on a scale, with a mean and standard deviation for each treatment condition. These summaries describe the reported ratings, while the contrast and its confidence interval describe how uncertain the estimated difference is. Neither the scale summary nor the comparison alone establishes the implications of the result for symptoms beyond the study task.

7. Results Posted in the Registry

• Inert Powder: mean 77.90 versus 80.80 on control; difference -2.90 (95% CI -12.61 to 6.81), standardized effect d = -0.21; z-test p = 0.558.

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.

Intensity of Pain

• 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:
  • Inert Powder: mean 81.90 versus 85.80 on control; difference -3.90 (95% CI -14.65 to 6.85), standardized effect d = -0.25; z-test p = 0.477.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Inert Powder and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary outcome: intensity of pain during cold-water hand immersion. It reports the outcome as a mean on a scale and gives a treatment contrast with an unadjusted p-value. As with the primary outcome, the posted mean contrast is lower in the inert-powder condition than in the aprepitant condition. This directional pattern does not align with the study hypothesis that aprepitant would be associated with lower symptom ratings.

The secondary endpoint relates to the primary question through the study rationale linking pain and dyspnea. However, pain intensity during hand immersion is a different measured experience and task from breathlessness during resistive load breathing. A pattern in one should not be treated as a substitute for the other, and the secondary outcome cannot establish the primary result.

Secondary results generally carry less evidential weight when they are not identified as the principal outcome and when the plan for handling multiple comparisons is not reported. Testing multiple outcomes can increase the chance that at least one result appears notable by chance. The registry labels the posted p-value as unadjusted, and it does not report a multiplicity procedure or a confirmatory hierarchy of outcomes. The secondary finding is therefore best viewed as descriptive rather than decisive.

The registry record does not report other secondary analyses, subgroup findings, or a detailed statistical plan. It is not possible to determine whether the pain outcome was prespecified in the original protocol, how it was incorporated into the analysis strategy, or whether any additional outcomes were assessed but not posted. The overall pattern offers no clear corroboration of the proposed direction, but the limited reporting and uncertainty do not support a strong conclusion about the relation between pain and breathlessness.

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

• Intensity of Pain

9. Statistical Interpretation

10. Statistical Methods Explained

What does the mean difference represent? A mean summarizes the central value of a continuous measurement. The registry reports a mean breathlessness rating for each treatment condition. The comparison is expressed as the inert-powder mean minus the aprepitant mean, so a negative estimate indicates a lower mean in the inert-powder condition. The sign depends on the order of subtraction; it does not change the underlying observations.

What does the standard deviation describe? A standard deviation describes how spread out individual observations are around their group mean. The posted standard deviations are 13.5 for aprepitant and 14.5 for inert powder. A larger standard deviation indicates more spread in the ratings, not a larger treatment difference. It also is not interchangeable with a confidence interval, which describes uncertainty in an estimated quantity.

What does a confidence interval add? A confidence interval gives a range of values reasonably compatible with the observed data under the assumptions of the analysis. The interval for the primary mean difference extends from -12.61 to 6.808. Because it includes zero, the data do not pin down the direction of the difference with precision. A confidence interval is not a range containing a fixed proportion of individual participants’ ratings, and it is not a probability statement about the true effect after the data have been observed.

How should the p-value be read? The unadjusted p-value is 0.558. In general, a p-value measures how unusual data at least as incompatible with a specified null model would be if that model and the analysis assumptions were correct. It does not measure the size or clinical importance of a difference, and it does not give the probability that the null hypothesis is true. Since the registry does not report the full analysis plan or model, the p-value should be interpreted alongside the posted estimate and interval rather than on its own.

Why does the crossover structure matter? In general, crossover studies observe participants under more than one treatment condition. This can permit comparisons that account for within-participant similarities, which may improve precision when handled appropriately. The analysis also may need to consider period and sequence effects, and whether effects from an earlier treatment could influence a later period. The registry identifies the study as crossover but does not report the statistical model, treatment sequence, washout details, or handling of these design features. The posted summary information is not enough to determine whether the reported contrast used paired observations or a crossover-specific analysis.

Why can over-dispersion matter? In general, over-dispersion means that observed variability is greater than a statistical model expects. If a model underestimates variability, its uncertainty intervals may be too narrow and its tests may be too optimistic. This concept is often especially relevant for counts, but the primary endpoint is continuous and is reported with means and standard deviations. The registry record does not report a model assessment or evidence of over-dispersion; it should not be assumed to have been assessed or present.

What is the role of adjustment? An adjusted analysis may account for design features or covariates specified in a statistical plan. In a crossover trial, a model could in principle address treatment, period, sequence, and within-participant correlation. General statistical practice cannot establish which approach this trial used. The registry record lists no reported analyses, and it does not report covariate adjustment or a prespecified model. The posted contrast should therefore be described as presented, without attributing an unreported adjustment to it.

What does an unadjusted result mean? The posted p-values are labeled unadjusted. In general, when several outcomes or comparisons are examined, each test creates an opportunity for a chance finding. Multiplicity procedures can control the overall chance of false-positive conclusions, depending on the testing strategy. The registry record does not report a multiplicity plan. This matters particularly for interpreting secondary outcomes; they are better treated as exploratory signals than as definitive confirmatory evidence when the adjustment strategy is unknown.

What do the reported summaries leave unanswered? Means and standard deviations describe the posted outcome data, but they do not disclose participant-level trajectories, missing observations, or the exact analysis set. The registry does not report how missing measurements were handled, whether any imputation was used, or whether all randomized participants were analyzed. The record also does not explain how repeated ratings were reduced to the time-weighted average. These details affect how fully the estimates can be independently evaluated.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of -2.9 units, with a confidence interval from -12.61 to 6.808. The interval extends across zero, so the posted results are compatible with a lower mean for inert powder, little or no difference, or a higher mean for inert powder. The breadth of the interval indicates that the estimate is not highly precise: the data do not closely locate the underlying contrast.

Precision is distinct from direction. The point estimate has a negative sign under the stated subtraction order, but the interval includes values on both sides of zero. It is therefore not appropriate to treat the point estimate alone as a settled direction or magnitude. The unadjusted p-value of 0.558 is consistent with the interval’s uncertainty, but it is not a substitute for considering the interval itself.

The standard deviations, 13.5 for aprepitant and 14.5 for inert powder, describe the spread of the posted ratings. They help characterize variability but do not directly show the uncertainty of the treatment contrast. Precision depends on factors including the amount of information, variability, and the analysis method. Because this is a crossover trial, the handling of within-participant observations can also affect the uncertainty estimate. That analysis detail is not reported in the registry record.

No threshold for a clinically important difference is reported. As a result, the interval cannot be classified against a trial-defined threshold for meaningful change. The interval describes statistical uncertainty in the mean difference under the analysis assumptions; it does not resolve the importance of possible differences for participants or establish the result for outcomes beyond the resistive load breathing task.

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 describe participants per arm for this continuous outcome, not total events. In general, a power calculation estimates the number of participants needed under specified assumptions to have a stated chance of detecting an effect of a chosen size if that effect is present. The 80% power column means planning for an 80% chance of detecting the selected effect under the calculation assumptions; the 90% column uses a higher target chance. These are design targets, not guarantees about what a future study will achieve.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The registry does not report the original trial’s sample-size assumptions or justification, so these illustrations should not be mistaken for the design basis of the completed trial. They are not observed power.

The planning scenarios consider 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The per-arm planning estimates increase as the target effect becomes smaller: a smaller difference is harder to distinguish from variability, so more participants are needed under the same assumptions. Raising the target power from 80% to 90% also requires a larger planned sample under the calculation framework.

These calculations use the observed effect as their starting point, so they are illustrative rather than a guarantee that the observed difference is the true effect. Their assumptions also describe equal allocation between arms, whereas the trial itself is identified as a crossover design. The calculations should be read according to their stated planning framework, not as a reconstruction of the trial’s original protocol.

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 = -2.900; pooled standard deviation σ = 14.009.
2. n = 2 × (1.96 + 0.842)² × 14.009² / -2.900² = 366.3, rounded up to 367 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 <- -2.89999999999999                      # observed difference in means
sigma <- 14.0089257261219                     # 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(1580423)
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 = 367 (80% power), 491 (90% power)
 75% of observed effect: n per arm = 652 (80% power), 872 (90% power)
 50% of observed effect: n per arm = 1,466 (80% power), 1,962 (90% power)
power.t.test: 367.3 
Simulated power at n = 367 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. Multiplicity, Missing Data and Analysis Populations

The registry lists one posted secondary outcome and labels its p-value as unadjusted. When researchers examine multiple outcomes or comparisons, the chance of at least one apparently positive finding can increase. A multiplicity plan can specify which outcomes are confirmatory, how tests are ordered, or whether significance thresholds are adjusted. Such a plan is not reported in the registry record. This limits how much weight to place on secondary findings, especially when interpreting isolated p-values.

The record reports three outcome measures but gives no reported analyses. It does not explain whether all specified outcomes were analyzed, whether all analyses were planned in advance, or how outcome reporting was selected. These points are not evidence that outcomes were omitted; they are details that are not reported in the registry record.

Missing-data methods are also not reported. The registry does not state whether any outcome observations were missing, how missing ratings were handled, whether imputation was used, or how participants with incomplete measurements were treated. Without these details, the effect of missingness on the posted estimates cannot be evaluated.

The analysis population is not specified. The record does not say whether the analysis followed an intention-to-treat approach, included only participants who completed both treatment periods, or used another population definition. Nor does it describe the handling of deviations from randomized treatment or incomplete crossover sequences.

For a crossover study, period and sequence effects, within-participant correlation, and possible carryover can be relevant to the analysis. The registry does not report the model or the approach used to address those issues. It also does not report whether interim analyses took place. These omissions limit the ability to assess the analysis strategy, but do not by themselves show that a particular procedure was or was not used.

15. 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 1% reporting threshold.

The registry reports zero serious adverse events in the aprepitant condition and zero in the inert-powder condition. It also reports zero other adverse events in each condition. The record lists 16 participants at risk for each treatment condition for these summaries.

These counts describe what was posted for the trial and its recorded observation period. They do not establish that no adverse events could occur, and they do not provide a precise estimate of uncommon risks. The registry does not report deaths; the death counts are not reported in the registry record. No serious adverse event terms are listed.

Safety findings should be interpreted in the context of the trial’s limited enrollment and the registry’s reporting detail. The record does not specify the full adverse-event collection procedures, follow-up duration for safety, or how events were attributed to treatment. The posted zero counts are therefore a description of reported events, not a broad safety conclusion.

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

The result is an estimate of the difference in mean breathlessness intensity during resistive load breathing, comparing inert powder with aprepitant. The estimated contrast was -2.9 units, and the confidence interval ran from -12.61 to 6.808. The estimate points toward lower mean ratings with inert powder, while the interval includes zero and values in either direction. The posted data therefore leave substantial uncertainty about the direction and size of the treatment difference.

The result does not demonstrate that the treatments are equivalent. A confidence interval that includes zero is not proof of no difference, and the unadjusted p-value of 0.558 does not establish that the null hypothesis is true. Conversely, the point estimate alone is not enough to establish that inert powder produces lower ratings. The estimate should be read together with its uncertainty and the limitations of the reported analysis details.

The trial’s hypothesis concerned lower breathlessness ratings with aprepitant compared with placebo during the specified task. The observed direction does not match that proposed direction, but the interval is broad enough that the data do not precisely determine the underlying contrast. The registry record does not report a threshold for a clinically important difference, so the result cannot be judged against a trial-defined level of meaningful change.

The findings are specific to the participants and conditions recorded: people with COPD undergoing resistive load breathing, with breathlessness measured by repeated Visual Analog Scale ratings. They do not directly answer questions about daily breathlessness, other clinical outcomes, long-term use, or other populations. Those outcomes are not reported in the registry record.

Finally, the registry identifies a randomized, quadruple-masked crossover design but does not describe the statistical model or how crossover features were handled. That missing analysis detail constrains interpretation of the posted comparison. The data are informative as a record of the observed means and their reported uncertainty, but they do not support a definitive claim for or against the proposed treatment effect.

17. Why This Trial Matters Statistically

This trial illustrates why an estimated effect and its precision need to be considered together. The posted point estimate gives a direction and scale for the observed mean contrast, while the confidence interval shows that the data do not tightly identify the underlying difference. Treating only the point estimate or only the p-value as the result would discard important information.

The crossover design also highlights the importance of reporting the analysis model. A crossover trial can make use of repeated treatment observations within participants, but interpretation depends on how that structure and any period or carryover considerations are handled. The registry identifies the design but does not describe those analytic choices. That gap matters because summary values alone cannot establish whether the comparison reflects a paired, crossover-specific analysis.

The secondary pain outcome connects statistically to the study’s biological and sensory rationale, while still measuring a different experience from breathlessness. Its unadjusted status and the lack of a reported multiplicity plan illustrate why secondary results are more appropriately interpreted as exploratory signals. A shared rationale does not make distinct outcomes interchangeable.

The sample-size illustrations also show that planning depends on the effect a study aims to detect: smaller target effects require more participants under the stated assumptions. Because the illustrations are based on the observed effect rather than the original design rationale, they should not be used to infer whether this completed trial was adequately planned or powered.

Overall, the record is a useful example of the difference between reporting an outcome and fully documenting the statistical path from design to inference. The posted means and interval allow a careful description of the observed result, while missing details about the analysis plan, missing data, and multiplicity limit stronger interpretation.

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.

The registry record provides limited detail about the conduct and analysis of this crossover trial. Although it identifies randomization and quadruple masking, it does not describe the allocation procedure, treatment sequence, masking roles, washout, or handling of period and possible carryover effects. These details are important for understanding whether the posted contrast reflects the design appropriately.

The analysis model and analysis population are not reported. It is therefore unclear from the registry record whether the comparison used within-participant pairing, whether participants with incomplete periods were included, or whether covariates were considered. Missing-data handling and the presence or absence of missing outcome observations are also not reported.

The primary outcome is based on repeated ratings, but the record does not explain the exact calculation of the time-weighted average or provide participant-level trajectories. The posted summaries do not show how ratings changed during the task. No threshold for a clinically important difference is reported, which limits assessment of the practical meaning of the estimated contrast.

The registry lists an enrollment of 16, and the confidence interval for the primary contrast is broad. This limits precision. The planning illustrations do not clarify the trial’s original design assumptions because the original sample-size justification is not reported in the registry record.

The record reports an unadjusted secondary result but no multiplicity plan or detailed analysis descriptions. It does not report interim analyses, and the absence of reported analyses means the statistical strategy cannot be fully evaluated. These reporting gaps do not establish that particular methods were absent; they mean that those methods are not documented in the registry record.

Finally, the primary outcome concerns a specific laboratory-like breathing task, and the secondary pain outcome concerns cold-water hand immersion. The registry does not report broader symptom, functional, or long-term outcomes. Conclusions should remain limited to the measures and conditions that are posted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Role of Substance P on Perception of Breathlessness During Resistive Load Breathing — NCT01580423.
• Registry record last updated 2013-07-19; status last verified 2013-05.
• Results first posted 2013-07-19.
• 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

The registry record describes a completed randomized, quadruple-masked crossover trial sponsored by Dartmouth-Hitchcock Medical Center. It lists 16 participants enrolled and compares aprepitant with inert powder in people with chronic obstructive pulmonary disease.

The primary outcome was time-weighted intensity of breathlessness during resistive load breathing, measured with a 100 mm Visual Analog Scale. The posted mean difference was -2.9 units for inert powder minus aprepitant, with a confidence interval from -12.61 to 6.808 and an unadjusted p-value of 0.558. The interval includes zero and leaves uncertainty about the direction and size of the difference.

The registry also posts intensity of pain during cold-water hand immersion as a secondary outcome. It does not report detailed analysis methods, missing-data handling, the analysis population, or the original sample-size justification. Safety summaries report zero serious and zero other adverse events in each treatment condition; deaths are not reported in the registry record.