Efficacy of Inhaling Bronchodilator Medications in Chronic Obstructive Pulmonary Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of Inhaling Bronchodilator Medications in Chronic Obstructive Pulmonary Disease (NCT01391559), a randomized na study. The primary outcome is Change in Forced Expiratory Volume in 1 Second (FEV1) From Baseline at Two Hours After Inhalation of the Study Medication.

2. Clinical Question

The rationale in the registry summary is that some people with COPD are uncertain whether they obtain clinical benefit from a dry-powder inhaler. One possible explanation described in the record is difficulty generating enough inspiratory flow to carry the medication into the lower respiratory tract. The trial therefore focused on people characterized as having low PIFR and compared delivery by nebulizer with delivery by dry-powder inhaler. The registry record does not report a separate eligibility threshold for low PIFR beyond the context described in its summary.

3. Trial Design

The registry describes a randomized, unmasked, crossover trial with enrollment of 20 participants. The interventions were arformoterol and salmeterol, both listed as drug interventions. In a crossover design, participants receive more than one study treatment in different periods, so comparisons can use information from the same participant under each treatment. As a general statistical principle, this can reduce the influence of stable differences between participants, although it also makes the analysis dependent on how treatment periods and within-person measurements are handled.

The record identifies the trial as completed. The recorded start was 2011-07 and primary completion was 2012-10. The sponsor was Dartmouth-Hitchcock Medical Center. The phase is listed as NA. These details describe the registry entry; they do not establish how treatment periods were scheduled or how long participants remained under observation.

The posted group summaries list 10 participants for arformoterol and 10 for salmeterol. The registry also reports an outcome analysis comparing the groups. Because the design is crossover, those group counts should not be interpreted as proof that there were separate sets of 10 participants assigned permanently to each treatment. The record does not report the treatment sequence, period structure, washout interval, or whether every participant completed both treatment periods. It also does not report a detailed account of withdrawals or exclusions.

The primary outcome was change in FEV1 from baseline at two hours after inhalation. No secondary outcome measures are posted. The registry’s reported analysis is a two-sided t-test of mean difference in final values, while the posted group summaries give means and standard deviations. The record does not report whether the sponsor’s analysis explicitly accounted for the crossover structure, treatment sequence, period, or within-participant correlation. That distinction matters because the analysis of a crossover study may use paired information rather than treating treatment groups as independent.

Masking is listed as none. The registry does not report further details about how participants, clinicians, or outcome assessors were informed of treatment allocation. Nor does it report the original sample-size justification or the design assumptions used to select enrollment. The planning estimates associated with the observed effect are a separate illustration and should not be taken as the original design rationale.

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: 26 patients screened: 5 excluded because did not meet exclusion criteria; 1 excluded because of exacerbation after visit 1.

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 Change in Forced Expiratory Volume in 1 Second (FEV1) From Baseline at Two Hours After Inhalation of the Study Medication, measured over 2 hours.

The primary endpoint measures the change in forced expiratory volume in one second (FEV1) from baseline at two hours after inhalation of the study medication. FEV1 is the volume of air a person can forcefully exhale during the first second of an expiratory maneuver. The registry reports the measure in mL and summarizes it as a mean with standard deviation.

FEV1 is used in respiratory research as a measure of airflow during forced expiration. In this trial, measuring it at a specified time after inhalation provides a way to compare the short-term change associated with the two inhaled medications. The endpoint fits the trial’s stated question about whether the delivery method and medication are associated with different lung-function measurements in participants with COPD and low PIFR.

The outcome is specific: it concerns FEV1 at two hours, not symptoms, everyday functioning, exacerbations, quality of life, or long-term disease outcomes. The registry does not report secondary outcomes. It also does not report details of the measurement procedure, the criteria for a valid spirometry measurement, or the handling of repeated measurements within the crossover periods. Those details would help readers assess how the outcome was collected and analyzed, but they are not reported in the registry record.

For arformoterol, the posted mean change was 84 mL with a standard deviation of 72 mL among 10 participants. For salmeterol, the mean change was 52 mL with a standard deviation of 105 mL among 10 participants. The standard deviations describe variation among observations; they are not confidence intervals for the treatment contrast. The estimate and uncertainty for the contrast address a different question: how precisely the difference between treatment summaries is estimated.

7. Results Posted in the Registry

• Salmeterol: mean 52.00 versus 84.00 on control; difference -32.00 (95% CI -110.91 to 46.91), standardized effect d = -0.36; z-test p = 0.427.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a mean difference describe?

The endpoint is continuous and is summarized by a mean. A mean difference compares the average outcome under one treatment with the average under another, with its sign depending on which treatment is subtracted from which. The posted means are 84 mL for arformoterol and 52 mL for salmeterol. The unadjusted recalculation expresses salmeterol relative to arformoterol, producing an estimate of -32 mL. The sponsor’s report gives 32 without interval bounds. Care is needed when comparing these figures because contrast direction and analysis method both affect how a result is presented.

In general, a mean summarizes the center of a set of measurements, while a standard deviation describes how spread out observations are around that mean. The posted standard deviations are 72 mL for arformoterol and 105 mL for salmeterol. A standard deviation is not the standard error of the treatment difference and is not a confidence interval. In a crossover study, the within-person relationship between measurements can affect the uncertainty of a contrast; separate group summaries do not show that relationship.

What does the reported t-test do?

The registry states that the sponsor used a two-sided t-test for mean difference in final values. In general, a t-test compares a mean difference with its estimated variability under a null hypothesis of no difference. A two-sided test considers departures in either direction. The registry gives a p-value of 0.17 but does not report confidence-interval bounds for that test. It also does not report details needed to determine whether this was a paired test, how crossover periods were handled, or whether any covariates were included.

The unadjusted recalculation is based on posted summary statistics rather than a participant-level crossover model. It reports an estimate of -32 mL, a 95% confidence interval from -110.9 to 46.91 mL, and p = 0.427. Such a recalculation can offer a transparent reference based on the available summaries, but it cannot recover the within-participant covariance or treatment-period information that is not present in those summaries. It should therefore be read as an unadjusted calculation, not as a reconstruction of every feature of the sponsor’s analysis.

How should a p-value be understood?

In general, a p-value is calculated under a statistical model and a null hypothesis. It describes the compatibility of the observed data with that null model, assuming the model’s conditions hold. It does not tell readers the probability that the null hypothesis is true, the probability that a result will replicate, or whether a difference is important to participants. The two p-values in the record are attached to distinct reported and recalculated analyses and should be kept with their respective methods.

The registry does not state a prespecified significance threshold for the trial’s own primary analysis. The sample-size planning illustration does list a two-sided significance level of 0.05, but that is an assumption for the illustration based on the observed effect, not evidence of the trial’s original analysis plan. The original design assumptions are not reported in the registry record.

Why does the crossover structure matter?

As a general concept, a crossover design compares treatments within participants across treatment periods. When the same person contributes measurements under both treatments, those measurements may be correlated. A paired analysis can use that correlation, while an analysis treating the observations as unrelated may not. The correct approach depends on the design and the data, including treatment sequence and period effects. The record identifies the trial as crossover but does not report the sequence, washout, period-level data, or whether the sponsor’s test used a paired method.

The posted recalculation is explicitly unadjusted and uses summary statistics. It cannot account for an unreported pairing structure. This limitation does not show that the sponsor’s analysis was incorrect; rather, the registry entry lacks the detail required to assess the relationship between the sponsor’s test and the crossover design. The sponsor’s analysis should be described as reported, without attributing additional modeling choices that the record does not specify.

What do the interval and spread add?

In general, a confidence interval gives a range of estimates compatible with the observed data under the calculation’s assumptions. Its width conveys precision: a wider interval indicates less precision than a narrower interval. The recalculated 95% interval ranges from -110.9 to 46.91 mL. Because it spans zero and extends in both directions, the recalculation does not precisely determine the direction or magnitude of the contrast.

Over-dispersion is a general concern when outcomes vary more than a model assumes; failing to account for excess variability can make uncertainty appear too small. The registry does not report an over-dispersion assessment, and the continuous endpoint is reported using means and standard deviations. The more directly relevant issue for this crossover comparison is that the participant-level pairing information is not available in the posted summaries.

What can the registry establish about the analysis?

The registry reports one primary outcome measure and one sponsor analysis. It does not report secondary analyses, a detailed statistical analysis plan, interim analyses, missing-data methods, analysis populations, or adjustment for multiple comparisons. These omissions should be treated as unreported details rather than filled in by assumption. The statistical summaries support a description of the posted short-term FEV1 results, but the record does not provide all the information needed to independently reproduce or fully evaluate the trial’s analysis.

10. Confidence Intervals and Precision

The unadjusted recalculation reports a mean difference of -32 mL for salmeterol relative to arformoterol, with a 95% confidence interval from -110.9 to 46.91 mL. The interval is wide and includes zero. Under the assumptions of this recalculation, the data therefore do not pin down the contrast precisely: values on either side of zero remain compatible with the estimate and its uncertainty. The interval should not be read as a guarantee that the true value lies within those limits, nor as a statement that all values inside it are equally plausible.

In general, a confidence interval combines a point estimate with information about its uncertainty. A narrower interval indicates greater precision, while a wider interval indicates that the estimate is less precise. The standard deviations in the posted group summaries—72 mL for arformoterol and 105 mL for salmeterol—describe variability in the outcome observations, not the uncertainty interval for the treatment contrast.

These interval limits come from an unadjusted recalculation based on the posted summary statistics. They do not incorporate participant-level crossover information that is not reported in those summaries. The registry’s sponsor-reported result gives a 95% confidence level but no lower or upper confidence-interval bounds. Consequently, the precision of the sponsor’s own estimate cannot be assessed from interval limits in the registry record.

The interval’s width is important when interpreting the point estimate. A point estimate alone can look more conclusive than the data warrant, especially with enrollment of 20. The recalculated uncertainty allows for a range of possible contrasts, rather than identifying a sharply defined effect. It also does not establish equivalence: the record does not report an equivalence margin or an equivalence analysis.

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 illustrate the approximate numbers that would be needed under the stated assumptions to detect specified fractions of the observed effect. The assumptions listed for this illustration 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 at the stated fraction of the observed effect. These are planning assumptions for the illustration; the original trial’s design assumptions are not reported in the registry record.

For 100% of the observed effect, the illustration gives 125 participants per arm for 80% power and 167 participants per arm for 90% power. For 75% of the observed effect, it gives 221 participants per arm for 80% power and 296 participants per arm for 90% power. For 50% of the observed effect, it gives 497 participants per arm for 80% power and 666 participants per arm for 90% power.

In plain language, the 80% power column describes the planned number per arm under which the assumed test would have an 80% chance of detecting the specified effect if that effect and the other assumptions were correct. The 90% power column describes the corresponding plan for a higher chance of detection. Smaller target effects require more participants because they are harder to distinguish from random variation. These figures are not observed power, and they are not the enrollment target used in the completed trial.

The estimates are illustrations based on the observed effect, not proof that the observed effect is stable or that a future study would have the same variability. The registry identifies the study as crossover, whereas the illustration states equal allocation between two arms; the record does not report whether the illustration incorporates crossover-specific features. Readers should interpret the planning values in light of those stated assumptions rather than as a definitive design recommendation.

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 = -32.000; pooled standard deviation σ = 90.025.
2. n = 2 × (1.96 + 0.842)² × 90.025² / -32.000² = 124.2, rounded up to 125 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 <- -32                      # observed difference in means
sigma <- 90.024996528742                     # 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(1391559)
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 = 125 (80% power), 167 (90% power)
 75% of observed effect: n per arm = 221 (80% power), 296 (90% power)
 50% of observed effect: n per arm = 497 (80% power), 666 (90% power)
power.t.test: 125.2 
Simulated power at n = 125 per arm: 0.801 (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. Analyses Reported by the Sponsor

The sponsor’s reported analysis is a two-sided t-test of mean difference in final values. It reports a mean difference of 32, a 95% confidence level, and p = 0.17. The registry does not provide the confidence-interval bounds for this result. The group summaries list a mean of 84 mL for arformoterol and 52 mL for salmeterol, each based on 10 participants.

The unadjusted recalculation expresses the contrast in the opposite direction, salmeterol relative to arformoterol, and reports -32 mL with a 95% confidence interval from -110.9 to 46.91 mL and p = 0.427. The sign difference is consistent with reversing the order of the contrast. The p-values are not the same because the recalculation is based on posted summary statistics and is not a reproduction of the sponsor’s analysis.

The record does not explain whether the sponsor’s test accounted for the crossover design or how the reported final values relate to the primary endpoint’s change-from-baseline description. Without participant-level data and further analysis details, the two analyses cannot be reconciled more fully. The discrepancy flag is false, but the sponsor’s result and the unadjusted recalculation should still be identified separately rather than presented as one test.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome measure and one reported analysis. It lists no secondary outcomes. The record does not report whether the trial had additional prespecified outcomes that were not posted, or whether the primary analysis was selected from among multiple analyses. No multiplicity adjustment or strategy is reported in the registry record.

In general, multiplicity arises when researchers perform multiple statistical tests or make several comparisons. As the number of tests increases, the chance of obtaining at least one apparently unusual result under a collection of null hypotheses can also increase. Methods such as prespecifying a primary comparison or adjusting inference may address this issue, but the registry does not report whether such measures were part of this trial’s analysis plan. It would be inappropriate to infer either that multiplicity was present or that it was controlled.

The record gives no missing-data method, number of missing primary-outcome measurements, or participant flow by treatment period. It does not state whether an intention-to-treat, per-protocol, or other analysis population was used. The blank population description for the primary outcome does not identify who was included in the analysis. These details matter because exclusions or incomplete crossover periods can affect both the estimate and its uncertainty.

The registry does not report an interim analysis plan, stopping rule, or whether any interim analyses were conducted. The original sample-size justification and the trial’s own statistical analysis plan are also not reported. The planning illustration based on the observed effect does not fill those gaps: it describes an illustrative calculation rather than the study’s original design rationale.

For a crossover trial, additional information is useful about treatment sequence, periods, washout, and how observations from the same participant were modeled. Those details are not reported. Their absence limits independent evaluation of whether the sponsor’s analysis and the unadjusted recalculation address the same estimand and uncertainty. These are limitations in what can be established from the registry record; they are not evidence that a particular method 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 lists 20 participants at risk for serious adverse events under arformoterol and 20 under salmeterol, with zero serious adverse events reported for each treatment. It also lists 20 at risk and zero other adverse events for each. The deaths field is not populated, so deaths are not reported in the registry record.

These figures describe the adverse-event entries in the registry. Because the study is identified as crossover, the treatment-specific at-risk counts should not be added together as though they necessarily represent separate participants. The record does not provide event definitions, collection procedures, follow-up duration, or details about whether participants contributed safety information during both treatment periods.

A zero count in this small trial means that no events of the listed type were posted for the stated at-risk group; it does not establish that an event cannot occur. The safety information should be interpreted as limited registry reporting, not as a comprehensive assessment of safety across settings or over longer periods.

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

The posted results describe a short-term comparison of change in FEV1 after inhalation of arformoterol solution or salmeterol dry powder among participants with COPD and low PIFR. The reported means were 84 mL and 52 mL, respectively, with standard deviations of 72 mL and 105 mL and 10 participants listed for each treatment. The sponsor reported a two-sided t-test p-value of 0.17 for a mean difference of 32. The unadjusted recalculation, expressed in the reverse contrast direction, estimated -32 mL with a 95% confidence interval from -110.9 to 46.91 mL and p = 0.427.

These results do not give a precise estimate of the treatment contrast. The recalculated interval includes zero and allows for contrasts in either direction. The sponsor’s report does not include interval bounds, and the registry does not provide enough analysis detail to establish how its test handled the crossover design. Neither p-value alone determines whether a difference is important to participants or whether treatments are equivalent.

The outcome is limited to FEV1 change measured two hours after inhalation. It does not directly report symptoms, daily function, longer-term lung-function change, exacerbations, or quality of life; no secondary outcomes are posted. The findings should therefore not be extended to outcomes that the registry did not measure.

The trial’s enrollment was 20. Its randomized crossover design may support within-participant comparisons when analyzed using the design information, but the registry does not report treatment sequence, washout, period-level measurements, or whether the sponsor’s analysis used paired information. The recalculation uses posted summary statistics and cannot recover unreported participant-level relationships.

Overall, the registry supports a cautious description of the short-term outcome summaries and the uncertainty of the unadjusted contrast. It does not support a broad conclusion about long-term outcomes, equivalence, or the full clinical value of either inhaler. The missing analysis details and limited precision are central to interpreting what these results can and cannot establish.

17. Why This Trial Matters Statistically

This trial raises a useful statistical question about matching an analysis to a study design. The registry calls the study randomized and crossover, but the readily reported treatment summaries are presented as groups with means, standard deviations, and 10 participants each. A crossover comparison can use within-person information; separate summaries do not show the correlation between a participant’s measurements on the two treatments. That information can materially affect the estimated uncertainty.

The contrast also illustrates why direction and method should be stated explicitly. The sponsor reports a mean difference of 32, while the unadjusted recalculation reports -32 mL for salmeterol relative to arformoterol. The sign reflects contrast order, while the differing p-values reflect that the two reported analyses are not the same calculation. Clear labeling helps prevent a reversal of direction from being mistaken for a substantive disagreement in the estimated means.

Precision matters alongside point estimates and p-values. The recalculated 95% confidence interval extends from -110.9 to 46.91 mL and includes zero, making the uncertainty visible. The sponsor’s result lacks reported interval bounds, which limits assessment of its precision. Reading estimates together with uncertainty avoids treating a single number or test result as a complete account.

The study also shows the distinction between an observed trial and planning calculations based on an observed effect. The planning illustration gives larger participant requirements for smaller target effects and higher power. It is not the trial’s original design justification and is not observed power. Keeping these roles separate prevents a post hoc planning illustration from being mistaken for evidence about the trial’s design or the certainty of its findings.

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 leaves several trial-specific questions unresolved. Although the design is identified as crossover, the treatment sequence, number and timing of periods, washout interval, and completion of both treatments are not reported. The sponsor’s analysis is described as a two-sided t-test of mean difference in final values, but the record does not state whether it was paired or otherwise modeled the within-participant structure. The posted summary statistics cannot recover that relationship.

The endpoint description specifies change from baseline at two hours, while the sponsor analysis is described as using final values. The registry does not explain how those descriptions correspond or provide enough detail to reproduce the sponsor’s analysis. Its reported 95% confidence level has no interval limits. The unadjusted recalculation has interval limits, but it is not a participant-level analysis of crossover data.

Enrollment was 20, and the posted treatment summaries list 10 participants each. The record does not report participant flow, missing measurements, exclusions, analysis populations, or missing-data methods. It also does not report the original sample-size justification or the trial’s own analysis plan. The planning illustration is based on the observed effect and should not be treated as a substitute for those design details.

The primary outcome is a short-term FEV1 measurement. No secondary outcomes are posted, and the registry does not provide longer-term outcomes or detailed safety follow-up. Masking is listed as none, but no further information about outcome assessment is reported. These limits concern the scope and reporting of the record; they do not establish that unreported procedures were absent or that the trial was conducted improperly.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy of Inhaling Bronchodilator Medications in Chronic Obstructive Pulmonary Disease — NCT01391559.
• Registry record last updated 2013-08-07; status last verified 2013-07.
• Results first posted 2013-08-07.
• 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 entry describes a completed randomized, unmasked crossover trial sponsored by Dartmouth-Hitchcock Medical Center. Enrollment was 20, and the condition was chronic obstructive pulmonary disease. The interventions were arformoterol solution delivered by nebulizer and salmeterol dry powder delivered by Diskus, studied in participants characterized as having low peak inspiratory flow.

The primary outcome was change in FEV1 from baseline at two hours after inhalation. The posted means were 84 mL for arformoterol and 52 mL for salmeterol. The sponsor reported a mean difference of 32 and p = 0.17, without confidence-interval bounds. An unadjusted recalculation in the reverse contrast direction gave -32 mL, a 95% confidence interval from -110.9 to 46.91 mL, and p = 0.427.

The registry does not report secondary outcomes, detailed crossover analysis methods, missing-data methods, analysis populations, or the original sample-size rationale. The results therefore describe a limited short-term endpoint with substantial uncertainty in the unadjusted contrast.