Efficacy and Safety of 3 Doses of Tiotropium Compared to Placebo in Adolescents (12 to 17 Yrs) With Moderate Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of 3 Doses of Tiotropium Compared to Placebo in Adolescents (12 to 17 Yrs) With Moderate Asthma (NCT01122680), a randomized phase 2 study. The primary outcome is Forced Expiratory Volume (FEV1) Peak (0-3h) Response.

2. Clinical Question

The clinical question is about a short-term lung-function response in a defined group of adolescents who still had symptoms while using controller treatment. It is not a question about every adolescent with asthma, longer-term outcomes, or treatment without background therapy. The registry record describes a randomized, double-blind, placebo-controlled trial with an incomplete crossover design. Participants were assigned within that design to treatment periods, but the registry record does not report the treatment sequences or explain which participants received which periods. The posted primary outcome uses the response from baseline at the end of a four-week treatment period. This page therefore interprets the reported lung-function estimates and their uncertainty, rather than drawing conclusions about outcomes that were not part of the posted results.

3. Trial Design

This was a Phase II randomized, double-blind, placebo-controlled trial using an incomplete crossover model. The registry record lists an enrollment of 105 participants and describes the population as adolescents aged 12 to 17 years with moderate persistent asthma. Participants were still symptomatic and not fully controlled with maintenance treatment; the brief description specifies continued use of an inhaled corticosteroid controller medication.

The trial compared tiotropium at 1.25 µg, 2.5 µg, and 5 µg with matching placebo. Each treatment was inhaled once daily in the evening using a Respimat inhaler. The official trial description identifies four-week treatment periods. “Incomplete crossover” means, in general, that participants do not necessarily receive every treatment in the study; the registry record does not report the sequences, allocation proportions, or the detailed transition arrangements. It also does not report whether a washout period was used, so no such feature should be assumed.

Randomization helps reduce systematic differences between assigned treatments, while double masking is intended to limit the influence of treatment knowledge on participant experience and outcome assessment. In a crossover design, observations across treatment periods can also be analyzed while accounting for the participant and period. Here, the primary outcome description says the analysis adjusted for treatment, period, patient, and baseline using a mixed model. These features are relevant to understanding the sponsor’s analysis, but they do not remove uncertainty from the estimates or replace details about the model that are not reported.

The registry record gives the trial status as completed. It does not report the original sample-size justification or the full statistical analysis plan. The planning illustrations on this page are separate from the trial’s original design assumptions.

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.

Period 1 (4 Weeks)

Reasons for not completing this period:

Period 2 (4 Weeks)

Reasons for not completing this period:

Period 3 (4 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full analysis set (FAS) is defined as patients randomised, treated, with baseline data and at least one on-treatment efficacy measurement after 4 weeks on treatment within a period. This patient set is therefore FAS reduced to patients with non-missing FEV1 data.

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 Forced Expiratory Volume (FEV1) Peak (0-3h) Response, measured over Baseline and 4 weeks.

The primary endpoint is the peak FEV1 response over the first three hours after dosing, assessed at the end of a four-week treatment period. FEV1 is the volume of air a person can forcefully exhale in the first second of an exhalation; in general, it is used as a measure of airflow and lung function. The endpoint is expressed in litres.

The response is defined in the registry record as the difference between the maximum FEV1 measured during the first three hours after dosing and the baseline FEV1 measurement. It is therefore a change-from-baseline measure, not simply the final FEV1 value. A positive response reflects a higher peak measurement relative to baseline, but the treatment comparison is the difference between the modeled responses for a tiotropium group and placebo.

Peak FEV1 is one way to summarize lung-function response during a specified window after a dose. It is not the only possible summary: the posted secondary outcomes include trough FEV1 and FEV1 averaged over the first three hours, as well as measures of forced vital capacity. Those measures describe different aspects of the recorded lung-function pattern. The primary endpoint is useful for a focused comparison, but it does not by itself establish effects on symptoms, daily functioning, longer-term control, or other outcomes that are not reported. The primary analysis population is defined as randomized and treated participants with baseline data and at least one on-treatment efficacy measurement after four weeks within a period, further restricted to those with non-missing FEV1 data.

7. Results Posted in the Registry

• Tio R1.25: mean 0.56 versus 0.49 on control; difference 0.07 (95% CI -0.06 to 0.20), standardized effect d = 0.17; z-test p = 0.313.
• Tio R2.5: mean 0.55 versus 0.49 on control; difference 0.06 (95% CI -0.07 to 0.19), standardized effect d = 0.14; z-test p = 0.391.
• Tio R5: mean 0.60 versus 0.49 on control; difference 0.11 (95% CI -0.02 to 0.24), standardized effect d = 0.28; z-test p = 0.086.

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.

Trough FEV1 Response

• 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:
  • Tio R1.25: mean 0.38 versus 0.29 on control; difference 0.09 (95% CI -0.03 to 0.22), standardized effect d = 0.24; z-test p = 0.148.
  • Tio R2.5: mean 0.35 versus 0.29 on control; difference 0.06 (95% CI -0.06 to 0.19), standardized effect d = 0.16; z-test p = 0.338.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tio R1.25 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 Tio R2.5 and the control. The interval gives the range of effects that remain compatible with the data.

FEV1 Area Under the Curve From 0 to 3 h (AUC0-3h) Response

• 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:
  • Tio R1.25: mean 0.46 versus 0.36 on control; difference 0.09 (95% CI -0.03 to 0.22), standardized effect d = 0.24; z-test p = 0.148.
  • Tio R2.5: mean 0.43 versus 0.36 on control; difference 0.07 (95% CI -0.05 to 0.20), standardized effect d = 0.18; z-test p = 0.265.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tio R1.25 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 Tio R2.5 and the control. The interval gives the range of effects that remain compatible with the data.

Forced Vital Capacity (FVC) Peak (0-3h) Response

• 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:
  • Tio R1.25: mean 0.55 versus 0.55 on control; difference 0.01 (95% CI -0.13 to 0.14), standardized effect d = 0.02; z-test p = 0.908.
  • Tio R2.5: mean 0.55 versus 0.55 on control; difference 0.01 (95% CI -0.13 to 0.14), standardized effect d = 0.02; z-test p = 0.907.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tio R1.25 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 Tio R2.5 and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes include other summaries of FEV1, measures of forced vital capacity, and forced expiratory flow. The displayed arm summaries for trough FEV1 and FEV1 area under the curve show higher response means in the tiotropium groups than in placebo. In contrast, the displayed forced vital capacity peak responses are close across the four groups. These broad patterns help put the primary endpoint in context: the secondary results do not all describe the same outcome dimension, and they should not be treated as interchangeable with peak FEV1.

These results are generally consistent with the primary endpoint in that some FEV1 summaries show a higher response in the active groups than placebo, while the pattern in the posted FVC peak summaries is much less separated. However, the secondary comparisons are simple recalculations from posted summaries, not sponsor-reported mixed-model analyses. No sponsor-reported analyses are listed for the secondary measures in this record. The secondary results therefore provide descriptive context, not a second, equally strong confirmation of the primary result.

There are multiple secondary outcomes and multiple potential group comparisons. In general, examining many results increases the chance that at least one looks notable by chance, especially if no adjustment or prespecified hierarchy is used. The registry record does not report a multiplicity procedure or identify a confirmatory order for the secondary tests. For that reason, unadjusted secondary results carry less weight than a primary analysis specified for the main question. The secondary outcome list is broader than the specific summary data; results for outcomes not displayed are not reported in the registry record.

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

• Trough FEV1 Response
• FEV1 Area Under the Curve From 0 to 3 h (AUC0-3h) Response
• FEV1 Individual Measurements Response at Each Time-point
• Forced Vital Capacity (FVC) Peak (0-3h) Response
• FVC Trough Response
• FVC Area Under the Curve From 0 to 3 h (AUC0-3h) Response
• FVC Individual Measurements at Each Time-point
• Forced Expiratory Flow (FEF) 25-75% Individual Measurements Response at Each Time Point

9. Statistical Interpretation

10. Statistical Methods Explained

What does a mean difference represent?

In general, a mean difference expresses how far apart two group averages are, in the units of the outcome. Here the outcome is the FEV1 response, measured in litres. A positive comparison estimate means the modeled response is higher in the named tiotropium group than in placebo. The estimate does not describe every participant; it summarizes the modeled group-level contrast. The registry record reports least-squares means for the arms and sponsor estimates described as mean differences in final values.

Why use a mixed model?

In general, a mixed model can represent both treatment effects and features of the study structure, such as repeated measurements or observations clustered within a participant. This is relevant to a crossover trial, where a participant may contribute data from more than one treatment period. For the primary outcome, the registry record says the analysis adjusted for treatment, period, patient, and baseline using a mixed model. The sponsor’s posted comparisons are described as mixed model repeated measures. These methods are designed to reflect the structure of the collected data rather than treating every measurement as independent.

The record does not provide the model formula, covariance structure, estimation details, or the assumptions used for handling missing measurements. Those details are not reported in the registry record. Consequently, the posted results can be described, but the model cannot be independently reconstructed from the summary information alone.

What does a standard error describe?

In general, a standard error describes the uncertainty in an estimated quantity, such as a group mean. It is not the same as the standard deviation of individual participant measurements. A smaller standard error usually indicates a more precise estimate under the model and assumptions used. The arm summaries list standard errors for the least-squares means. The sponsor’s comparison intervals are based on its mixed-model analysis and need not match intervals constructed from those arm-level standard errors using a simpler method.

Why do the recalculated results differ?

The simple recalculations on this page use posted arm-level summary statistics to form unadjusted comparisons. They are approximate because the pooled standard deviations are inferred from the reported standard errors, and they do not reproduce the sponsor’s model adjustments for treatment, period, participant, and baseline. The sponsor’s analysis uses the trial’s mixed-model repeated-measures approach and takes precedence when the two results differ. The recalculated values are useful as a transparent check on the reported summaries, not as a replacement for the trial analysis.

For the primary endpoint, the posted sponsor estimate for 5 µg versus placebo is 0.113 L, with a 95% confidence interval from 0.036 to 0.190 and p = 0.004. The simple recalculation has the same rounded point estimate but a confidence interval from -0.016 to 0.242 and an unadjusted p-value of 0.086. A matching point estimate does not make the inferential results equivalent: the interval and p-value depend on how uncertainty is estimated and what features of the design are accounted for.

How should p-values be read?

In general, a p-value summarizes how compatible the observed data are with a specified null model, under the analysis assumptions. It is not the probability that the null hypothesis is true, nor does it measure the size or practical importance of an effect. The sponsor reports p-values for the three comparisons with placebo. The p-values for comparisons among active doses are not reported in the posted results. The record also does not report whether the sponsor adjusted these tests for multiple comparisons, so the p-values should not be read as if a particular multiplicity procedure had necessarily been used.

What does the crossover structure add?

In general, crossover designs can compare treatments while using within-participant information, because the same participant may be assessed during different treatment periods. This can reduce the influence of stable differences between participants when the design and analysis are appropriate. An incomplete crossover means not all participants necessarily receive all treatments. In this trial, the primary outcome description explicitly includes treatment, period, patient, and baseline in the mixed model. However, the registry record does not report enough design detail to evaluate treatment sequence allocation, carryover handling, or the exact pattern of missing periods. Those unknowns limit a fuller audit of the analysis.

The estimates and uncertainty should therefore be understood as results from the posted model and its population, with the simple recalculations serving only as approximate unadjusted summaries. General statistical interpretation cannot fill in the unreported specifications of the trial’s model or analysis plan.

11. Confidence Intervals and Precision

A confidence interval describes a range of values compatible with the data and analysis, under the model assumptions. In general, a narrower interval indicates greater precision, while a wider interval leaves more uncertainty about the size and direction of the difference. A 95% confidence interval is not a guarantee that the true value lies inside the particular interval; it is a procedure with a long-run coverage interpretation under its assumptions.

For the sponsor-reported primary comparison of 5 µg versus placebo, the estimated difference is 0.113 L and the 95% confidence interval extends from 0.036 to 0.190 L. The interval lies above zero. The sponsor’s reported comparisons for 1.25 µg and 2.5 µg versus placebo have intervals that include zero. Those intervals therefore leave uncertainty about whether the corresponding differences are positive or negative, as well as about their magnitude. The active-dose comparisons also have intervals that include zero.

The simple recalculated intervals are wider than the corresponding sponsor-reported intervals for the placebo comparisons. This reflects that the recalculations are unadjusted approximations based on posted summary statistics, whereas the sponsor reports a mixed repeated-measures analysis. Since the record flags a discrepancy, the sponsor’s own analysis takes precedence. The recalculated intervals should not be used to overwrite or relabel the sponsor’s results.

Precision is distinct from clinical importance. The registry record does not state a threshold for a clinically important FEV1 difference, so the confidence intervals cannot be classified against such a threshold. The primary outcome is one measure at the end of a four-week treatment period; the intervals do not quantify uncertainty about unreported outcomes or longer-term results. The estimates are also based on the stated analysis population, rather than necessarily on every participant enrolled.

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 are planning illustrations based on the observed effect in the posted summaries, not the trial’s own original design calculations. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting the stated fraction of the observed effect. For these continuous outcomes, the figures are participants per arm, not a total across both arms and not total events. The original trial’s sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true effect. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm. These are planning quantities, not a retrospective measure of how much power the completed trial had. This is not observed power.

The table also scales the assumed effect to 100%, 75%, and 50% of the observed effect. A smaller effect is harder to distinguish from random variation under the same assumptions, so smaller effects need more participants. This relationship is shown by the larger planning figures for the smaller fractions in the table. The observed effect may itself be uncertain, so planning from it does not guarantee that a future study will see the same effect or have the anticipated precision.

Because this trial used an incomplete crossover design, the simple equal-allocation, two-arm illustrations should not be mistaken for a reconstruction of its design. They are standardized comparisons for planning, not a statement about the actual number randomized to each treatment sequence. The trial’s original sample-size rationale, including any assumptions about the crossover structure, is not reported in the registry record.

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 = 0.067; pooled standard deviation σ = 0.403.
2. n = 2 × (1.96 + 0.842)² × 0.403² / 0.067² = 567.8, rounded up to 568 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.0670000000000001                      # observed difference in means
sigma <- 0.40295051463099                     # 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(1122680)
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 = 568 (80% power), 761 (90% power)
 75% of observed effect: n per arm = 1,010 (80% power), 1,352 (90% power)
 50% of observed effect: n per arm = 2,272 (80% power), 3,041 (90% power)
power.t.test: 568.8 
Simulated power at n = 568 per arm: 0.800 (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. Analyses Reported by the Sponsor

The sponsor reports the primary comparison using a mixed model for repeated measures. For the 5 µg dose versus placebo, the reported mean difference in final values is 0.113, with a 95% confidence interval from 0.036 to 0.190 and p = 0.004. The 1.25 µg and 2.5 µg placebo comparisons are also reported with their model-based estimates, confidence intervals, and p-values. The sponsor’s analysis is the trial’s own reported inferential analysis.

The simple recalculations shown alongside the posted results use unadjusted comparisons reconstructed from summary statistics. For the 5 µg comparison, the point estimate is also 0.113, but the recalculated interval is from -0.016 to 0.242 and the unadjusted p-value is 0.086. The recalculated intervals for the other comparisons also differ from the sponsor’s reported intervals. These differences are expected to matter because the recalculation does not reproduce the mixed model’s adjustment for treatment, period, patient, and baseline, and its uncertainty estimates are approximate.

The discrepancy flag means the sponsor’s own analysis takes precedence. The recalculations are not a competing trial analysis and should not be used to replace the sponsor’s results. They offer a simple, transparent check based on the displayed arm summaries, while the sponsor’s model-based results account for the stated repeated-measures structure. The registry record does not provide enough model detail to reproduce the sponsor’s results exactly.

15. Multiplicity, Missing Data and Analysis Populations

The trial includes three tiotropium doses compared with placebo, along with pairwise comparisons among active doses and a set of secondary outcomes. In general, testing many comparisons raises a multiplicity concern: even when no treatment difference exists, the chance of at least one apparently unusual result can increase as the number of tests grows. Common approaches include prespecifying a primary comparison, controlling an overall error rate, or treating secondary findings as exploratory. The registry record does not report the multiplicity strategy, if any, used for the primary dose comparisons or the secondary outcomes. The sponsor’s reported p-values should therefore be read as posted, without assuming a particular adjustment.

The registry record defines the primary analysis population as randomized and treated participants with baseline data and at least one on-treatment efficacy measurement after four weeks within a period, further restricted to participants with non-missing FEV1 data. It also reports outcome-specific group counts for the primary endpoint. These counts are not the same as the overall enrollment and reflect the population contributing to the posted endpoint summaries.

Missing data handling can affect estimates, particularly when the chance of missing an outcome is related to participant characteristics or response. In general, mixed models can use available repeated measurements under assumptions about the missingness process, but the validity of that approach depends on the assumptions and implementation. The registry record does not report the amount or reasons for missing primary outcome data, the method used to handle missing measurements, or sensitivity analyses examining missingness. It is therefore not possible from the posted record to assess how robust the estimates are to alternative missing-data assumptions.

The registry record also does not report the full statistical analysis plan, detailed model specification, treatment-sequence information, or analysis decisions made before results were examined. These omissions limit evaluation of whether all analyses followed a prespecified plan. They do not invalidate the posted estimates, but they are relevant when interpreting several comparisons and the precision of the results.

16. 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 5% reporting threshold.

Most frequent serious adverse event terms

Serious events with the highest arm-level rate: h1n1 influenza (1.3%), pneumonia mycoplasmal (1.3%), asthma (1.3%), presyncope (1.2%).

The posted serious adverse event counts are 0 of 75 for placebo, 1 of 75 for the 1.25 µg dose, 0 of 75 for the 2.5 µg dose, and 1 of 80 for the 5 µg dose. These are counts among the listed participants at risk for serious adverse events. The registry record lists no participants affected by other adverse events in any of these groups. The deaths field is not populated, so deaths are not reported in the registry record.

These figures describe events recorded during this trial; they are not a complete safety assessment for other populations or longer periods. In general, low event counts leave substantial uncertainty about uncommon events, and the counts alone cannot establish whether an event was caused by a treatment. The registry record also lists serious-event terms with percentages, including H1N1 influenza, pneumonia mycoplasmal, asthma, and presyncope. The posted summary does not link those listed terms to specific treatment groups, so no group-specific interpretation should be inferred from them.

Safety findings should be read alongside the trial’s limited size and four-week treatment periods, not as a guarantee that an event will or will not occur. The record does not provide additional detail about event timing, severity beyond the serious-event classification, or causal attribution.

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

The posted results address a specific question: the short-term change in peak FEV1 after dosing, at the end of a four-week treatment period, among adolescents with moderate persistent asthma who remained symptomatic on maintenance therapy. The sponsor’s mixed-model analysis estimates a positive difference for the 5 µg dose versus placebo, with a 95% confidence interval above zero. The reported estimates for the other placebo comparisons have intervals that include zero. These are findings about the measured endpoint and the reported analysis population.

They do not establish that every participant experienced a response like the group average. They do not show that all three doses have the same effect, or that active doses are equivalent to one another. Nor do they establish a difference in symptoms, daily activity, asthma control, exacerbations, long-term outcomes, or any other outcome not reported. The record does not report a threshold for a clinically important change in FEV1, so the statistical estimates cannot be translated into a judgment about clinical importance using this record alone.

The results should also not be generalized automatically beyond the trial population. The study concerns adolescents in the specified age range with moderate persistent asthma who were not fully controlled on maintenance treatment, and treatment was added to an inhaled corticosteroid controller. The record does not establish what would happen in other age groups, disease severities, treatment settings, or over longer periods.

Finally, the sponsor’s model-based analysis and the simple recalculations answer the same broad comparison using different methods. Because their uncertainty estimates differ, the sponsor’s own analysis takes precedence. Neither the sponsor’s p-value nor the unadjusted recalculation is a measure of the probability that a treatment works. The estimates and intervals are the relevant description of the posted statistical evidence, with the limitations of the record kept in view.

18. Why This Trial Matters Statistically

This trial is statistically interesting because it combines an incomplete crossover design with several dose comparisons and repeated outcome measurements. In general, crossover designs can make efficient use of within-participant observations, while also requiring analysis that accounts for the treatment period and participant structure. The primary outcome description says that the mixed model adjusted for treatment, period, patient, and baseline, making those design features directly relevant to interpretation.

The results also illustrate why a model-based trial analysis cannot always be recreated from group summaries alone. The sponsor’s reported 5 µg comparison has the same rounded point estimate as the simple recalculation, but the confidence intervals and p-values differ. The difference illustrates that the analysis method and its treatment of repeated measurements and study structure can affect uncertainty and inference. Reporting both the sponsor result and a clearly labeled unadjusted recalculation helps readers see the distinction without treating the latter as a substitute.

Another statistical lesson is that the conclusions vary by comparison and outcome. The sponsor’s model-based estimate for the highest dose versus placebo is more clearly separated from zero than the estimates for the other placebo comparisons, while the secondary summaries do not all show the same degree of separation. This is why interpretation should follow the prespecified primary question where available and avoid elevating isolated secondary findings.

The record also highlights what is needed for stronger independent assessment: the full model specification, missing-data details, multiplicity approach, and original sample-size rationale are not reported. Their absence does not erase the observed results, but it constrains reproducibility and the ability to judge the robustness of multiple comparisons.

19. 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 posted results have several trial-specific limitations. First, the primary analysis population is narrower than the overall enrolled group: participants needed to be randomized and treated, have baseline data, and contribute at least one on-treatment efficacy measurement after four weeks within a period, with non-missing FEV1 data. The registry record does not provide the reasons or patterns of missingness, so it is not possible to determine from this summary whether missing measurements could have influenced the estimates.

Second, the design is described as an incomplete crossover, but the record does not give treatment sequences, period-specific participant counts, or details about treatment transitions. Although the outcome description says the primary model adjusted for treatment, period, patient, and baseline, the model specification and assumptions are not reported. This limits independent reconstruction of the analysis and assessment of possible sequence or carryover concerns.

Third, the sponsor’s analysis and the approximate, unadjusted recalculations have differing confidence intervals and p-values. The sponsor’s analysis takes precedence, but its model cannot be fully reproduced from the posted summary. The recalculations are not a substitute for participant-level or model-level information.

Fourth, several doses and secondary endpoints were examined, while the multiplicity strategy is not reported in the registry record. Secondary outcomes also do not have sponsor-reported analyses in the posted results. Their unadjusted pattern should be considered exploratory rather than treated as a set of confirmatory tests.

Finally, the endpoint reflects a short-term lung-function response at the end of a four-week treatment period. The record does not provide a clinical-importance threshold for the endpoint or results for longer-term outcomes. These limitations restrict the scope of conclusions that can be drawn from this trial record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of 3 Doses of Tiotropium Compared to Placebo in Adolescents (12 to 17 Yrs) With Moderate Asthma — NCT01122680.
• Registry record last updated 2014-05-16; status last verified 2012-07.
• Results first posted 2012-06-27.
• 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.

23. Record Summary

This completed Phase II trial enrolled 105 adolescents aged 12 to 17 years with moderate persistent asthma. It compared once-daily evening tiotropium at 1.25 µg, 2.5 µg, and 5 µg with matching placebo in a randomized, double-blind, incomplete-crossover design, on top of maintenance inhaled corticosteroid controller therapy.

The primary endpoint was peak FEV1 response, defined as the difference between baseline and the maximum FEV1 measured within three hours after dosing at the end of a four-week treatment period. The sponsor reported a positive mixed-model difference for 5 µg versus placebo, with a 95% confidence interval above zero; the intervals for the other placebo comparisons included zero. Simple recalculations differ in uncertainty estimates and are approximate, so the sponsor’s own analysis takes precedence.

The record does not report the original sample-size justification, multiplicity strategy, detailed missing-data handling, or full model specification. The posted safety counts include one serious adverse event in each of the 1.25 µg and 5 µg groups and none in the placebo or 2.5 µg groups. These results describe the posted short-term outcomes and should not be extended to unreported outcomes or populations.