Teaching Use of Respiratory Inhalers (TURI): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Teaching Use of Respiratory Inhalers (TURI) (NCT01456494), a randomized na study. The primary outcome is Number of Participants Misusing Metered-Dose Inhaler (MDI) Post Education Between Teach to Goal (TTG) and Brief Intervention (BI).

2. Clinical Question

The registry describes a feasibility study intended to assess whether patients could be enrolled and randomized to the two educational approaches, while also collecting preliminary estimates of their comparative effectiveness. The investigators’ stated hypothesis was that Teach-to-Goal would increase patients’ ability to learn inhaler technique compared with Brief Intervention. They planned to examine that hypothesis separately for the metered-dose inhaler and Diskus devices.

The primary outcome is specifically the count of participants misusing a metered-dose inhaler after education; it is not a direct measure of long-term inhaler use, clinical control, or health events. The registry gives the measurement timeframe as one hour at the initial hospital visit. It does not report the operational definition used to classify technique as misuse, so the exact criteria behind that classification are not reported in the registry record.

3. Trial Design

TURI is a randomized, parallel-group study of two educational approaches to respiratory inhaler technique. The registry lists the allocation as randomized and masking as single. It does not specify who was masked, so that detail is not reported in the registry record. The study is marked completed, with enrollment of 50. The registry lists asthma and COPD as the conditions and identifies the University of Chicago as the sponsor.

The two arms differed in the teaching strategy. Teach-to-Goal used repeated cycles of instruction and assessment, including demonstration and teach-back, continuing until the skill was mastered according to the arm description. Brief Intervention consisted of verbal and written instruction without demonstration or repeated instruction rounds. The registry classifies both interventions as other rather than assigning a drug-treatment category.

The primary endpoint concerns metered-dose inhaler misuse one hour into the initial hospital study visit. The study description also identifies a separate hypothesis for Diskus technique, but a numerical Diskus result is not reported among the detailed outcome results. The registry lists a study start of 2009-07 and primary completion of 2010-03. It records the phase as NA.

The arm-level primary results include 24 participants in Teach-to-Goal and 26 in Brief Intervention. For the primary outcome, the posted counts of participants classified as misusing the metered-dose inhaler are 3 and 12, respectively. These are observed outcome counts, not measures of how many people were initially approached, eligible, or assigned but later excluded. Those participant-flow details and the trial’s original statistical design assumptions are not reported in the registry record.

The registry’s stated purpose combines feasibility with preliminary comparative estimates. It does not report a formal sample-size justification, detailed randomization procedures, or an analysis plan. The methods used to generate the posted comparisons are also not described in the 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.

Initial Inpatient Visit

Follow-Up Visit (Post 30-day Discharge)

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 Number of Participants Misusing Metered-Dose Inhaler (MDI) Post Education Between Teach to Goal (TTG) and Brief Intervention (BI), measured over 1 hour at the V0-V1 initial hospital study visit.

The primary endpoint is the number of participants recorded as misusing a metered-dose inhaler after education. The registry describes the outcome as a participant count and gives the timeframe as one hour at the initial hospital study visit. In the Teach-to-Goal arm, the posted count is 3 among 24 participants; in the Brief Intervention arm, it is 12 among 26 participants.

Technique is a proximal outcome: it assesses inhaler use soon after the educational session rather than a later clinical event or a long-term measure of health. Counting participants classified as misusing the device offers a direct way to compare the recorded technique outcome between the two education groups at the specified visit. It is also consistent with the study’s stated aim of collecting preliminary estimates of comparative educational effectiveness.

The count alone does not describe the precise technique error, how misuse was assessed, or how a participant was classified. The registry does not give those criteria, and they are not reported in the registry record. Nor does this endpoint measure sustained technique after leaving the hospital, actual medication adherence, or changes in asthma or COPD outcomes. Those broader outcomes should not be inferred from a short-term technique measure. The endpoint is therefore best read narrowly: it is a count of participants assessed as misusing an MDI at the stated post-education timeframe.

7. Results Posted in the Registry

• Brief Intervention: 46.2% (12/26) versus 12.5% (3/24) on control; risk difference 33.7 percentage points (95% CI 10.4 to 56.9), risk ratio 3.69 (1.18–11.51); unadjusted two-proportion z-test p = 0.009.

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.

Number of Participants Reporting Acute Health-related Events 30 Days Post Hospital Discharge Between TTG and BI

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Brief Intervention: 40.0% (8/20) versus 5.3% (1/19) on control; risk difference 34.7 percentage points (95% CI 11.0 to 58.4), risk ratio 7.60 (1.05–55.14); unadjusted two-proportion z-test p = 0.010.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Brief Intervention than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Self-reported Confidence With Inhaler Technique Versus Actual Technique

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Brief Intervention: 27.8% (5/18) versus 33.3% (6/18) on control; risk difference -5.6 percentage points (95% CI -35.6 to 24.5), risk ratio 0.83 (0.31–2.24); unadjusted two-proportion z-test p = 0.717.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Brief Intervention and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address distinct questions beyond immediate MDI technique: reported acute health-related events after discharge, Diskus misuse, and the relationship between confidence and observed technique. The posted numerical results cover the 30-day acute-event outcome and confidence relative to actual technique. The record lists Diskus misuse and the 90-day acute-event outcome among the secondary outcomes, but numerical results for these are not reported in the registry record.

The secondary findings add context, but they do not directly replicate the primary endpoint. The primary result concerns MDI misuse one hour after education; the 30-day outcome concerns health-related events after discharge, while the confidence measure compares a self-report with actual technique. Their different definitions and timeframes mean that their estimates cannot be read as interchangeable measures of the same educational effect.

The 30-day comparison has a positive risk difference and an unadjusted p-value of 0.01, while the confidence comparison has an unadjusted p-value of 0.717 and an interval spanning negative and positive values. These are exploratory comparisons in a record that does not report a multiplicity adjustment or a complete analysis plan. Testing or estimating several outcomes increases the chance that at least one result will look noteworthy by chance, particularly when results are considered without adjustment. Unadjusted secondary findings therefore carry less weight than a prespecified, fully documented confirmatory analysis.

The secondary results are best treated as preliminary signals that can inform questions for later study, rather than as independent proof of a broad effect across technique, confidence, and health events. The registry does not report a formal hierarchy for the secondary outcomes or the intended strategy for interpreting them together. Their relationship to the primary result is therefore descriptive: they concern related aspects of the study’s educational question, but the record does not establish that a change in one outcome caused a change in another.

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

• Number of Participants Misusing Diskus Post Education Between TTG and BI
• Number of Participants Reporting Acute Health-related Events 30 Days Post Hospital Discharge Between TTG and BI
• Differences in the Prevalence of Reported Acute Health-related Events 90 Days Post Hospital Discharge Between TTG and BI
• Self-reported Confidence With Inhaler Technique Versus Actual Technique

9. Statistical Interpretation

10. Statistical Methods Explained

The outcomes in this study are binary at the participant level: each person is classified according to whether the specified event or condition was recorded. The registry reports counts of participants with the outcome, along with the group sizes. For the primary MDI outcome, that means the count classified as misusing the device in each randomized arm, rather than a continuous score of technique quality.

What does the risk difference express?

A risk difference compares the proportions with an outcome in two groups by subtracting one group’s proportion from the other. It is expressed on the proportion scale, so it describes an absolute difference rather than a relative change. For the primary result, the posted risk difference is 0.337 for Brief Intervention compared with Teach-to-Goal. Its positive sign reflects a higher observed outcome proportion in Brief Intervention under the comparison’s stated direction. The registry does not explain the statistical procedure used to calculate this estimate or its interval.

How do relative measures differ?

A risk ratio compares the outcome proportions as a ratio, while an odds ratio compares the odds of the outcome. Both are relative measures and answer a different descriptive question from the risk difference. For the primary comparison, the posted risk ratio is 3.692, with a confidence interval from 1.184 to 11.51; the posted odds ratio is 6.0, with a confidence interval from 1.429 to 25.19. Relative measures can appear large even when based on limited observations, and their uncertainty should be read with their intervals rather than their point estimates alone. No particular measure should be treated as the only meaningful summary.

What does a confidence interval communicate?

A confidence interval describes the uncertainty around an estimated effect under the method used to construct it. Narrower intervals represent greater precision, while wider intervals indicate that a broader range of effect sizes remains compatible with the data and method. An interval is not a range containing a known fixed proportion of individual outcomes, and it does not account automatically for bias, missing data, or an unsuitable analysis model. The registry does not report which interval method was used for these comparisons.

How should the p-value be read?

A p-value measures how unusual data at least as incompatible with a specified null hypothesis would be under the assumed statistical model. Smaller values indicate greater incompatibility with that null under those assumptions. It does not give the probability that the null hypothesis is true, measure the size or importance of an effect, or replace the confidence interval. The primary comparison has an unadjusted p-value of 0.009. Because the registry does not report the test procedure, model, or multiplicity strategy, the result should be interpreted as the posted unadjusted comparison rather than as a fully documented confirmatory analysis.

Why does over-dispersion matter?

Over-dispersion is a concern in some count models when observed variability exceeds what a model assumes. It can make model-based standard errors too small and confidence intervals too narrow if ignored. This trial’s outcomes are presented as participant counts for binary outcomes, and the record does not report a count-model analysis or an over-dispersion assessment. The concept is relevant generally, but there is no basis in the registry record to say that over-dispersion affected these results.

What is not described about the analysis?

The registry includes arm-level results and posted comparisons, but it does not list reported analysis methods in its analysis records. The analysis population, handling of missing outcomes, covariate adjustment, and any prespecified modeling choices are not reported in the registry record. The posted comparisons therefore allow a descriptive reading of the available summaries, but do not reveal the full analysis pathway or whether the results were adjusted for other factors.

11. Confidence Intervals and Precision

The primary risk difference is 0.337, with a 95% confidence interval from 0.104 to 0.569. The estimate is positive, and both reported limits are above zero. The interval nevertheless spans a range of effect sizes, so the point estimate should not be treated as a precisely known difference. Its width reflects uncertainty in the comparison, which is expected to be important when outcome counts and group sizes are limited.

The relative summaries are also imprecise. The primary risk ratio is 3.692, with a confidence interval from 1.184 to 11.51, while the odds ratio is 6.0, with a confidence interval from 1.429 to 25.19. The broad ranges show that the estimated relative contrast is uncertain. The risk difference and relative measures are on different scales, so their numerical magnitudes should not be compared as if they expressed the same quantity.

Precision also differs across the secondary comparisons. For the 30-day acute health-related event outcome, the risk difference is 0.347, with a confidence interval from 0.110 to 0.584. For confidence relative to actual technique, the risk difference is -0.056, with a confidence interval from -0.356 to 0.245. The latter interval crosses zero and includes both negative and positive differences, leaving the direction uncertain.

Confidence intervals address sampling uncertainty under the analysis method, but they do not correct for incomplete outcome collection, measurement error, or bias in trial conduct. The registry does not identify the interval method or provide participant-flow and missing-data details. These omissions limit how fully the precision figures can be evaluated.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size planning figures are illustrations based on the observed effects, not the trial’s original design assumptions. The original design assumptions are not reported in the registry record. The planning calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider detecting the stated fraction of the observed effect. For these outcomes, the displayed values are participants per arm, not total events.

The 80% power column gives the illustrated number of participants per arm for a future study to have an 80% chance of detecting the chosen effect under the stated planning assumptions, if that effect and assumptions were correct. The 90% power column expresses the corresponding planning target for a 90% chance. These are design targets, not guarantees about the result of a future study.

Rows for planning for 75% or 50% of the observed effect ask what would be needed if a future study aimed to detect a smaller effect than the observed estimate. Smaller effects are harder to distinguish from random variation, so they generally require more participants. For the primary outcome, for example, the posted planning figures are 28 participants per arm for 80% power and 37 for 90% power when planning for 100% of the observed effect. For 75% of the observed effect, the corresponding figures are 46 and 60; for 50%, they are 91 and 121.

These figures are planning illustrations, not observed power. They do not show the probability that the completed study detected an effect, and they do not establish that the observed effect is a stable estimate for future research. A curve, when read alongside the figures, represents how the planning requirement changes with the effect targeted under the stated assumptions. It should be read as a planning aid, not as further trial outcome evidence.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.125; treatment proportion p₁ = 0.462; average p̄ = 0.293.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6438 = 1.2619.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5982 = 0.5035.
4. n = (1.2619 + 0.5035)² / (0.3365)² = 27.5, rounded up to 28 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
p0 <- 0.125                          # control proportion
p1 <- 0.461538461538462                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(1456494)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 28 (80% power), 37 (90% power)
 75% of observed effect: n per arm = 46 (80% power), 60 (90% power)
 50% of observed effect: n per arm = 91 (80% power), 121 (90% power)
power.prop.test: 27.5 
Simulated power at n = 28 per arm: 0.822 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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 names several secondary outcomes in addition to the primary endpoint. It does not report a multiplicity plan describing whether or how the analyses were prioritized, adjusted, or interpreted as a family of comparisons. The posted p-values for the detailed secondary comparisons are unadjusted. When multiple outcomes are examined, the chance of observing at least one apparently unusual result can increase, even when there is no underlying difference. This is why unadjusted secondary results should be considered exploratory unless a clear prespecified strategy is documented.

The registry record does not report an analysis plan, a prespecified outcome hierarchy, or which analysis population was intended for each outcome. It also does not report whether comparisons were adjusted for baseline characteristics or other factors. These details matter because they affect what the estimates represent and how confidently they can be interpreted.

Participant counts differ across outcomes. The primary comparison includes 24 participants in Teach-to-Goal and 26 in Brief Intervention; the 30-day outcome uses 19 and 20, and the confidence outcome uses 18 and 18. These different denominators make it important not to assume that every randomized participant contributed to every outcome. Reasons for the variation, missing-data definitions, and methods for handling missing observations are not reported in the registry record.

The record also does not report whether analyses followed an intention-to-treat approach, whether participants were excluded after randomization, or how withdrawals and incomplete assessments were handled. Without those details, the available summaries cannot establish whether missingness could have influenced the comparisons. The registry does not report interim analyses or stopping rules. That absence should not be filled by assumptions about how the study was conducted.

Together, the missing analysis and missing-data details limit assessment of potential bias and the confirmatory status of the results. The arm-level summaries remain useful descriptions of what was posted, but their interpretation should acknowledge that the registry record does not fully document how the estimates were produced.

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 safety figures list 0 serious adverse events in each arm and 0 other adverse events in each arm. The reported deaths are 0 in Teach-to-Goal and 3 in Brief Intervention. The at-risk counts listed for these safety summaries are 24 and 26, respectively.

These are counts in the registry record. They do not, by themselves, establish whether an event was caused by an educational intervention, and the record does not provide event descriptions or a causal assessment. The serious adverse event terms are not listed. The registry also does not report further detail about the timing, circumstances, or relationship of the recorded deaths to study participation.

Safety counts should be read separately from the primary technique outcome. A zero count in a group does not prove that an event could not occur, and a nonzero count does not establish causation. The available figures are limited to the recorded totals and group sizes; they do not support a detailed comparative safety analysis.

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

The primary result describes a short-term difference in the number and proportion of participants recorded as misusing an MDI after the two educational approaches. The observed counts are 3 among 24 participants in Teach-to-Goal and 12 among 26 participants in Brief Intervention. The posted risk difference is 0.337, with a confidence interval from 0.104 to 0.569. These findings characterize the participants and assessment represented in the registry record.

They do not show whether participants maintained correct technique after leaving the hospital, whether medication use changed, or whether asthma or COPD outcomes improved. The endpoint was measured one hour into the initial hospital visit. Long-term technique and clinical outcomes are not established by that measurement. The registry describes feasibility and preliminary comparative estimates as study aims, so the estimates should be interpreted in that context.

The comparison also does not prove that the teaching approach caused the observed difference. Randomized allocation is a useful design feature for comparing groups, but interpretation still depends on execution, outcome measurement, missing data, and analysis choices. The record does not provide enough detail to assess all of those features. It does not report the criteria for classifying technique as misuse, who was masked, or how incomplete outcomes were handled.

The result should not be generalized automatically to all patients with asthma or COPD, other care settings, other inhaler devices, or different teaching delivery. The sample comprises the participants enrolled in this study, and the registry does not provide a broader representativeness assessment. Numerical results for some listed secondary outcomes are not reported in the registry record.

Thus, the defensible conclusion is descriptive: the posted short-term MDI outcome differed between the study arms, with uncertainty reflected in the interval. The record does not establish the durability, mechanism, clinical consequences, or broader applicability of that observed difference.

17. Why This Trial Matters Statistically

This trial is statistically informative because it separates a practical feasibility aim from preliminary estimation of a group contrast. Feasibility studies can help establish whether recruitment and randomization are workable while producing early estimates that may guide future study planning. Those estimates can be useful, but they are often uncertain and may not represent the effect that a later, larger study would observe.

The outcome is also a clear example of the distinction between absolute and relative comparisons. The risk difference expresses an absolute contrast in outcome proportions, while the risk ratio and odds ratio express relative contrasts. Each answers a different statistical question. Reporting several measures can provide context, but broad confidence intervals remind readers that the apparent magnitude is not known precisely.

Differences in outcome denominators are another important feature. The primary result and secondary results do not all use the same participant counts. Recognizing that distinction discourages treating every outcome as if it were measured in the same complete cohort. Without details about missingness and analysis populations, a reader should avoid inferring why those denominators differ.

Finally, the study illustrates why an unadjusted secondary p-value should not be read in isolation. Several outcomes are named, but the registry does not report a strategy for multiplicity or a full analysis plan. A seemingly small p-value on one secondary outcome can be less persuasive when many questions are considered and the analysis context is unclear. The most useful statistical reading keeps the primary result, its uncertainty, the feasibility purpose, and the incomplete reporting context together.

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.

Several limitations specific to this registry record affect interpretation. The primary endpoint is assessed one hour after education, which does not establish whether technique persisted beyond the initial hospital visit. The registry does not report the detailed criteria used to classify MDI misuse, making it difficult to assess exactly what errors counted as the outcome or how consistently the assessment was applied.

The record does not identify who was masked, despite listing the study as single-masked. It also does not describe the randomization procedure, allocation concealment, or the analysis method. These omissions prevent a complete assessment of safeguards against bias and of how the posted estimates were calculated.

Participant counts vary by outcome, and the reasons for those differences are not reported in the registry record. The record does not explain missing-data handling, exclusions, or the analysis population. It also does not provide numerical results for the listed Diskus misuse and 90-day acute-event outcomes, limiting the ability to assess the full set of intended questions.

The registry describes the study as intended to assess feasibility and collect preliminary comparative estimates, but does not report its original sample-size justification or the basis for the target enrollment. Planning illustrations based on observed effects cannot replace those original design details. The registry also does not report a complete statistical analysis plan or a multiplicity strategy. These limitations make the posted comparisons useful as preliminary descriptions, while restricting claims about precision, confirmatory evidence, and broader applicability.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Teaching Use of Respiratory Inhalers (TURI) — NCT01456494.
• Registry record last updated 2019-06-18; status last verified 2018-05.
• Results first posted 2019-06-18.
• 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 TURI registry record describes a completed randomized, parallel-group study comparing Teach-to-Goal education with Brief Intervention among participants with asthma or COPD. Enrollment is listed as 50, and the sponsor is the University of Chicago. The primary endpoint is the number of participants misusing an MDI one hour after education at the initial hospital study visit.

The posted primary counts are 3 among 24 participants in Teach-to-Goal and 12 among 26 in Brief Intervention. The risk difference is 0.337, with a 95% confidence interval from 0.104 to 0.569 and an unadjusted p-value of 0.009. Detailed secondary results are posted for 30-day acute health-related events and confidence relative to actual technique; numerical results for the listed Diskus and 90-day outcomes are not reported in the registry record.

The record also lists safety counts, but does not report a complete analysis plan, missing-data approach, or multiplicity strategy. The results are best read as preliminary estimates from a feasibility-focused study, with uncertainty and reporting limitations kept in view.