Asthma Clinical Research Network (ACRN) Trial - Tiotropium Bromide as an Alternative to Increased Inhaled Corticosteroid in Patients Inadequately Controlled on a Lower Dose of Inhaled Corticosteroid (TALC): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Asthma Clinical Research Network (ACRN) Trial - Tiotropium Bromide as an Alternative to Increased Inhaled Corticosteroid in Patients Inadequately Controlled on a Lower Dose of Inhaled Corticosteroid (TALC) (NCT00565266), a randomized phase 3 study. The primary outcome is Change Between Week 14 and Week 0 in the Morning (AM) Peak Expiratory Flow (PEF).

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, quadruple-masked, crossover trial of three asthma treatment regimens. The registry lists enrollment of 210 participants. In a crossover design, participants receive more than one treatment over successive periods, so comparisons can reflect within-participant changes as well as differences between treatment periods. The registry describes three treatment periods, each lasting 16 weeks, with the order of regimens varying across randomized sequences.

The regimens were tiotropium plus lower-dose inhaled corticosteroid, salmeterol plus lower-dose inhaled corticosteroid, and a higher dose of inhaled corticosteroid alone. The posted primary endpoint analysis uses change from week 0 to week 14 during each period. Thus the described treatment period and the primary outcome measurement window are not identical in length. The registry record does not report why the analysis used that measurement window.

The trial began in 2008-05, had primary completion in 2010-05, and is listed as completed. Milton S. Hershey Medical Center is named as the sponsor. The registry identifies all randomized participants as included in the linear mixed-effects model analysis for the primary outcome. It does not report the model's detailed specification, including how it handled treatment sequence, period, carryover, or within-participant correlation. Those details are important in crossover studies, and cannot be inferred from the design label alone.

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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: All randomized participants were included in the linear mixed-effects model analysis

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 Between Week 14 and Week 0 in the Morning (AM) Peak Expiratory Flow (PEF), measured over AM PEF was measured daily during each of the three 14-week treatment periods. The primary analysis constructed the change between week 14 and week 0..

The primary endpoint was the change between week 0 and week 14 in morning (AM) peak expiratory flow, measured in liters per minute. Peak expiratory flow is a measure of how rapidly a person can exhale air. The registry says AM PEF was measured daily during each of the three treatment periods, and that the primary analysis constructed a change from the beginning to the end of the specified measurement window.

A change score focuses on how the measured value shifts over a treatment period rather than only comparing measurements at a single time. In a crossover trial, the same participant contributes measurements under different regimens, allowing treatment comparisons to draw on repeated observations from that participant. A linear mixed-effects model can be used to account for correlated measurements, although the registry record does not report the model details needed to determine exactly how this was done.

Morning peak flow is one way to quantify respiratory function, and repeated daily measurements can characterize changes over time. It is not the only aspect of asthma control. For that reason, the registry also lists symptom, lung-function, quality-of-life, control, rescue-medication, and control-day outcomes. The registry record does not state a threshold for a clinically meaningful change in peak flow, so the numerical differences should be interpreted as estimated changes on the measured scale rather than as proof of a particular clinical importance.

7. Results Posted in the Registry

• LABA + 1xICS: mean 18.00 versus 24.40 on control; difference -6.40 (95% CI -16.75 to 3.95), standardized effect d = -0.12; z-test p = 0.225.
• 2xICS: mean -1.40 versus 24.40 on control; difference -25.80 (95% CI -36.52 to -15.08), standardized effect d = -0.46; z-test p = <0.001.

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.

Change Between Week 14 and Week 0 in the Forced Expiratory Volume in One Second (FEV1)

• 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 errors.
• Result:
  • LABA + 1xICS: mean 0.01 versus 0.12 on control; difference -0.11 (95% CI -0.18 to -0.04), standardized effect d = -0.30; z-test p = 0.002.
  • 2xICS: mean 0.02 versus 0.12 on control; difference -0.10 (95% CI -0.17 to -0.03), standardized effect d = -0.28; z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for LABA + 1xICS than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for 2xICS than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change Between Week 14 and Week 0 in Asthma Symptoms

• 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 errors.
• Result:
  • LABA + 1xICS: mean -0.04 versus -0.09 on control; difference 0.05 (95% CI 0.00 to 0.10), standardized effect d = 0.19; z-test p = 0.050.
  • 2xICS: mean 0.03 versus -0.09 on control; difference 0.12 (95% CI 0.07 to 0.17), standardized effect d = 0.46; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for LABA + 1xICS than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for 2xICS than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change Between Week 14 and Week 0 in the Asthma Quality-of-life Questionnaire Score

• 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 errors.
• Result:
  • LABA + 1xICS: mean 0.28 versus 0.15 on control; difference 0.13 (95% CI -0.02 to 0.28), standardized effect d = 0.17; z-test p = 0.090.
  • 2xICS: mean 0.05 versus 0.15 on control; difference -0.10 (95% CI -0.25 to 0.05), standardized effect d = -0.13; z-test p = 0.199.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between LABA + 1xICS and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 2xICS and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover several domains: lung function measured by FEV1, asthma symptoms, quality of life, asthma control, rescue albuterol use, and the proportion of asthma control days. The posted numerical results include estimates for FEV1, symptoms, and quality of life. The registry record lists the other outcomes, but their results are not reported in the registry record.

Across the posted secondary estimates, the direction and strength of the contrasts are not uniform across measures. The FEV1 estimates show a different pattern from the quality-of-life estimates, and the symptom comparisons show evidence that varies by comparator. This variation means the secondary outcomes do not form a single consistent numerical pattern that can be reduced to one conclusion. Scale direction and the meaning of a change also differ across measures, so numerical signs should be interpreted in the context of each outcome's scoring.

These findings provide additional information about the range of measured outcomes, but they do not replace the primary endpoint. The primary question concerned AM PEF, while secondary measures address related but distinct aspects of asthma and participant experience. Agreement across outcomes can add context; disagreement may reflect real differences between domains, variation, or chance. The registry record does not state that these secondary comparisons were adjusted for multiple testing or identify a prespecified ordering among them.

Unadjusted secondary p-values carry less weight when many endpoints and comparisons are considered. Testing more hypotheses without an adjustment or a prespecified hierarchy increases the opportunity for chance findings to appear statistically notable. The absence of reported multiplicity handling does not prove that none was used, but the method is not reported in the registry record. Secondary estimates are therefore best read as exploratory context, with attention to their intervals and the fact that the posted pairwise comparisons are recalculated from summary statistics.

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

• Change Between Week 14 and Week 0 in the Forced Expiratory Volume in One Second (FEV1)
• Change Between Week 14 and Week 0 in Asthma Symptoms
• Change Between Week 14 and Week 0 in the Asthma Quality-of-life Questionnaire Score
• Change Between Week 14 and Week 0 in the Asthma Control Questionnaire Score
• Change Between Week 14 and Week 0 in the Albuterol Rescue Puffs Per Day
• Change Between Week 14 and Week 0 in the Proportion of Asthma Control Days

9. Statistical Interpretation

10. Statistical Methods Explained

The registry identifies the primary measure as a least-squares mean change and gives standard errors as the measure of dispersion. A least-squares mean is a model-based estimate of an average outcome. Unlike a raw arithmetic mean, it can reflect adjustment for variables included in the statistical model. The registry record says that a linear mixed-effects model was used and that all randomized participants were included in that model, but it does not state which covariates or design factors were included.

A mixed-effects model can represent both systematic differences and correlation among repeated observations. In this trial, participants received three regimens in sequence, and AM PEF was measured repeatedly. Measurements from the same participant are generally related rather than independent. A mixed model can account for that dependence through participant-level effects and can also include other terms, depending on the analysis plan. The registry record does not report the model formula or the particular terms used, so it is not possible to verify how treatment, period, sequence, or possible carryover were handled.

The arm estimates are least-squares mean changes, while the pairwise mean differences and confidence intervals are marked as recalculated. They are simple, unadjusted recalculations from the posted summary statistics. The recalculated uncertainty uses approximate standard deviations derived from the reported standard errors, rather than the covariance structure from the trial's crossover model. Consequently, these comparisons are useful for a basic reading of the posted summaries but are not equivalent to a participant-level, model-based treatment contrast. The registry record does not list sponsor-reported pairwise analyses for these comparisons.

What does a confidence interval describe?

A confidence interval describes uncertainty in an estimated contrast under the assumptions of the method used to construct it. In repeated use of the same method under its assumptions, intervals at a stated confidence level would cover the underlying quantity at that rate. It is not a range containing a stated proportion of individual participant outcomes, and it does not assign a probability to the true effect after the data are observed. Here, the posted contrast intervals are unadjusted recalculations, so their interpretation depends on the approximations used to construct them.

What does an unadjusted p-value mean?

A p-value measures how incompatible the observed data are with a specified null hypothesis under a statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The posted p-values are unadjusted. When several outcomes or treatment comparisons are examined, the chance of at least one apparently unusual result can increase if no multiplicity strategy is used. The registry record does not report a multiplicity adjustment for the results.

Why does crossover structure matter?

In a crossover trial, each participant receives multiple interventions, so treatment comparisons can use repeated measurements from the same people. That structure may improve precision when within-participant measurements are strongly related, but it also makes the analysis depend on how period effects, sequence, and correlation are represented. A simple comparison of arm-level means does not reproduce all features of a crossover analysis. The registry record's statement that a linear mixed-effects model included all randomized participants does not give enough detail to assess those features.

What does the standard error show?

A standard error describes the estimated variability of an estimate across repeated samples under a model. It is not the standard deviation of individual participant measurements. Smaller standard errors generally correspond to more precise estimates, while larger standard errors signal greater uncertainty. The primary outcome arm estimates have standard errors of 4.2, 3.2, and 3.5 liters per minute, respectively. Because those are arm-level standard errors, they should not be treated as the standard deviation of participants' changes.

The registry record does not report the trial's original sample-size justification, its prespecified statistical analysis plan, or interim analyses. Those omissions prevent a determination of the original design assumptions and whether the posted comparisons follow a prespecified hierarchy. The planning illustrations are separate from that missing information and use an explicitly stated set of assumptions described with the sample-size results.

11. Confidence Intervals and Precision

Precision is reflected in the range of estimates compatible with the data under the interval method. For the AM PEF comparison between tiotropium plus lower-dose inhaled corticosteroid and salmeterol plus lower-dose inhaled corticosteroid, the recalculated unadjusted interval extends from -16.75 to 3.949 liters per minute. Because zero lies within this interval, the posted summaries are compatible with no difference as well as with differences in either direction. The point estimate alone should not be read as a precise estimate of the contrast.

For the comparison with higher-dose inhaled corticosteroid, the recalculated interval extends from -36.52 to -15.08 liters per minute. It lies on the negative side of zero for the comparator-minus-reference contrast, but the range still spans a range of possible magnitudes. An interval excluding zero addresses compatibility with a zero contrast under the method; it does not determine whether the difference is clinically important. The registry record does not report a clinical-importance threshold.

The confidence intervals are recalculated from posted summary statistics, and the standard deviations used for that calculation are approximate. The primary analysis itself is described as a linear mixed-effects model, but its pairwise results are not posted in the registry record. Therefore these intervals do not reflect every possible feature of the original crossover analysis. The distinctions matter: statistical precision under a simplified recalculation is not the same as certainty about the treatment contrast under a fully specified trial model.

Secondary endpoints also have intervals with varying widths. Intervals that include no difference leave substantial uncertainty about the direction or size of the contrast; intervals that exclude no difference still need to be considered alongside endpoint selection and multiplicity. A confidence interval is most informative when interpreted with the estimate, the scale, the analysis method, and the design that generated the observations.

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 table and curve give planning illustrations, not the number of participants actually analyzed. Because the outcomes are continuous, the figures are participants per arm, not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The illustrated effect to detect is a stated fraction of the observed effect. These are planning calculations based on the observed effect, not the trial's original design assumptions, which are not reported in the registry record.

The 80% power column gives the number of participants per arm estimated to provide an 80% chance of detecting the assumed effect under those planning assumptions if that effect is real. The 90% power column gives the corresponding planning number for a 90% chance. These are design targets, not guarantees for a future study; actual results depend on the true effect, variability, analysis, and other design features. The figures are not observed power.

Rows that plan for 75% or 50% of the observed effect assume a smaller contrast than the full observed effect. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm as the assumed effect becomes smaller. The large changes in required sample size across the rows show why planning from a single observed estimate can be sensitive to the assumed effect. The illustrated calculations compare two arms and do not reproduce the crossover structure or the mixed-effects analysis described for this trial.

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 = -6.400; pooled standard deviation σ = 54.105.
2. n = 2 × (1.96 + 0.842)² × 54.105² / -6.400² = 1,121.9, rounded up to 1,122 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 <- -6.4                      # observed difference in means
sigma <- 54.1054525902889                     # 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(565266)
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 = 1,122 (80% power), 1,502 (90% power)
 75% of observed effect: n per arm = 1,995 (80% power), 2,671 (90% power)
 50% of observed effect: n per arm = 4,488 (80% power), 6,008 (90% power)
power.t.test: 1122.9 
Simulated power at n = 1,122 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 a primary endpoint and several secondary outcomes, but it does not report a statistical plan describing how the family of comparisons was handled. In particular, a multiplicity adjustment, testing hierarchy, or designation of confirmatory versus exploratory secondary outcomes is not reported in the registry record. The posted pairwise p-values are unadjusted. When multiple endpoints and treatment contrasts are examined, interpreting each p-value as if it were the only test can overstate the strength of evidence. The registry information does not establish whether a separate plan addressed this issue.

Missing-data methods are also not described in sufficient detail. The registry states that all randomized participants were included in the linear mixed-effects model analysis for the primary outcome. That describes the analysis population, but it does not specify how missing measurements, missed visits, or incomplete treatment periods were handled. It does not report imputation, assumptions about why observations might be missing, or sensitivity analyses. The number randomized to each regimen is reported as 210 in the arm summaries, but that does not establish that complete outcome measurements were available for every participant at every period.

The registry record does not report interim analyses, stopping rules, the original sample-size justification, or a detailed prespecified statistical analysis plan. Without those details, it is not possible to determine the planned treatment of multiplicity, missing observations, or analysis deviations. No assumptions about those procedures should be inferred from the presence of model-based estimates.

The distinction between the primary model and the recalculated comparisons also matters. The primary outcome analysis is described as a linear mixed-effects model, while the contrast estimates discussed in the posted results are simple unadjusted recalculations. Those recalculations do not disclose how missing repeated measurements were handled in the original model and do not recreate its covariance structure. The registry record reports no sponsor pairwise analyses to compare against these recalculations.

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 2.5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: unrelated events (2.0%), hospitalization due to pneumonia (1.0%).

The registry reports serious adverse events by treatment group among participants listed as at risk. The figures are 3 affected participants among 203 at risk for tiotropium plus lower-dose inhaled corticosteroid, 4 among 196 for salmeterol plus lower-dose inhaled corticosteroid, and 4 among 195 for higher-dose inhaled corticosteroid. These are participant counts, not a measure of event severity beyond the registry's serious-event classification, and they should be read with the corresponding at-risk group size.

Other adverse events are listed separately: 2 affected participants among 203 at risk in the tiotropium group, 2 among 196 in the salmeterol group, and 6 among 195 in the higher-dose inhaled corticosteroid group. The registry's listed serious-event terms include “unrelated events” at 2.0% and “hospitalization due to pneumonia” at 1.0%. These term percentages are reported as registry entries; the record does not give further detail about timing or attribution in this summary.

Deaths are not reported in the registry record. Adverse-event counts are descriptive and do not, on their own, establish a comparative safety difference. In a crossover design, participants may experience more than one treatment period, and the registry summaries do not explain how events were attributed across periods or analyzed for comparisons.

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

The posted primary outcome shows positive estimated changes in AM PEF for tiotropium plus lower-dose inhaled corticosteroid and for salmeterol plus lower-dose inhaled corticosteroid, while the estimate for higher-dose inhaled corticosteroid is negative. In the recalculated contrast with salmeterol, the confidence interval includes no difference. In the contrast with higher-dose inhaled corticosteroid, the interval lies below zero for the stated comparator-minus-reference direction. These are statements about the posted estimates and their unadjusted precision, not treatment recommendations.

The results do not establish that two regimens are equivalent when an interval includes zero. They also do not establish clinical importance solely because an interval excludes zero or a p-value is small. The registry record gives no clinical threshold for an important AM PEF change. Interpretation should therefore retain both the estimated magnitude and uncertainty, along with the limitations of the simple recalculations.

The trial's crossover structure means participants received multiple treatments. Its primary analysis is described as a linear mixed-effects model including all randomized participants, but model details and the sponsor's pairwise analyses are not reported. The recalculated comparisons use posted summary statistics and do not reproduce a complete analysis of repeated, within-participant data. This limits how directly those comparisons can be interpreted as the trial's definitive treatment contrasts.

The registry also lists several secondary outcomes, but their results are incomplete and multiple-testing procedures are not reported. Those outcomes can add context but cannot be treated as independent confirmation without considering the number of comparisons and the analysis plan. The safety entries are descriptive, and deaths are not reported in the registry record.

Overall, the posted data describe estimates of change and uncertainty for the specified outcomes. They do not establish a complete account of clinical benefit, harm, or treatment choice. The missing detail on model specification, missing data, multiplicity, and original design assumptions is relevant to how confidently the numerical contrasts can be generalized beyond the summary results.

17. Why This Trial Matters Statistically

This trial illustrates why a study's design and its summary statistics need to be read together. The crossover design has participants receive each of three regimens in different orders, creating repeated measurements that are not independent. A mixed-effects model is identified for the primary analysis, but the registry does not report its detailed specification. That makes the design's statistical features important to interpretation rather than incidental background.

It also illustrates the difference between a model-based primary outcome estimate and an unadjusted contrast reconstructed from summary statistics. The latter can help readers understand the scale and direction of the posted results, but it cannot account for all the information in participant-level repeated measurements. Confidence intervals and p-values are meaningful only in relation to the method used to calculate them.

The multiple outcome domains raise a further statistical issue. Lung function, symptoms, quality of life, and control measures capture related but distinct experiences. A pattern across outcomes can help assess consistency, but multiple unadjusted comparisons make isolated statistical findings less definitive. Without a reported multiplicity strategy or analysis hierarchy, secondary results need cautious interpretation.

Finally, the planning illustrations show how sample-size needs depend on the assumed effect. The participant counts increase when planning for smaller effects, emphasizing the uncertainty that can arise when an observed effect is used as the basis for future planning. Those illustrations are not the original trial design justification. Together, these features make the record useful for discussing estimation, repeated-measures analysis, and the limits of interpreting unadjusted results.

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 summary leaves several trial-specific details unavailable. Although it identifies a linear mixed-effects model for the primary analysis and says all randomized participants were included, it does not describe the model terms, covariance structure, handling of treatment sequence or period, or assessment of carryover. Those details matter in a crossover study with repeated measurements.

The primary pairwise estimates and confidence intervals discussed in the statistical summary are unadjusted recalculations from posted arm-level summary statistics, with approximate standard deviations. They do not reproduce the full participant-level analysis. The registry reports no sponsor analysis entries for these comparisons. Thus the recalculations should not be mistaken for a complete report of the trial's inferential analysis.

The registry lists six secondary outcomes, but only three have numerical results in the posted results. Results for asthma control, albuterol rescue puffs, and the proportion of asthma control days are not reported in the registry record. A multiplicity plan is not reported, and the secondary comparisons are unadjusted. The record also does not report missing-data procedures, sensitivity analyses, interim analyses, or the original sample-size justification.

The treatment descriptions identify three 16-week periods, while the primary endpoint is constructed from week 0 to week 14 measurements. The rationale for this analysis window is not reported. The registry does not state a threshold for a clinically meaningful AM PEF change, which limits interpretation of whether an estimated difference is important beyond its statistical scale.

Safety summaries give counts of affected participants and selected serious-event terms, but do not provide enough detail in this summary to characterize event timing or treatment attribution in the crossover sequence. Deaths are not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Asthma Clinical Research Network (ACRN) Trial - Tiotropium Bromide as an Alternative to Increased Inhaled Corticosteroid in Patients Inadequately Controlled on a Lower Dose of Inhaled Corticosteroid (TALC) — NCT00565266.
• Registry record last updated 2018-07-02; status last verified 2018-05.
• Results first posted 2013-04-09.
• 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

This completed Phase 3 trial randomized 210 participants with asthma in a quadruple-masked crossover comparison of tiotropium plus lower-dose inhaled corticosteroid, salmeterol plus lower-dose inhaled corticosteroid, and higher-dose inhaled corticosteroid. Each participant was assigned a sequence of three treatment periods. The primary endpoint was change in morning peak expiratory flow from week 0 to week 14.

The primary analysis is described as a linear mixed-effects model including all randomized participants. Posted arm estimates are least-squares mean changes with standard errors. Pairwise contrasts discussed in the statistical interpretation are unadjusted recalculations from summary statistics, rather than posted sponsor analyses. Their uncertainty should be read with that distinction in mind.

The registry lists six secondary outcomes, with numerical results posted for three. Multiplicity procedures, missing-data methods, detailed model terms, and the trial's original sample-size justification are not reported in the registry record. The sample-size illustrations are separate planning calculations based on stated assumptions and the observed effect.