Randomised, Double- Blind, Cross-over Efficacy and Safety Comparison of Three Different Doses of Tiotropium Administered Once Daily Versus Placebo in Patients With Moderate Persistent Asthma.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Randomised, Double- Blind, Cross-over Efficacy and Safety Comparison of Three Different Doses of Tiotropium Administered Once Daily Versus Placebo in Patients With Moderate Persistent Asthma. (NCT01233284), a randomized phase 2 study. The primary outcome is Forced Expiratory Volume in One Second (FEV1) Peak Within 0-3 Hours Post-dose Response.

2. Clinical Question

The trial was designed to assess efficacy and safety for three doses of tiotropium added to inhaled corticosteroids in people with moderate persistent asthma who were not fully controlled on their maintenance treatment. The primary outcome was a lung-function measure: the response in FEV1, or forced expiratory volume in one second, measured as the peak within zero to three hours after dosing. The record also describes additional lung-function outcomes and pharmacokinetic sampling in a subset.

The central comparison is each dose against placebo, rather than a direct test of one tiotropium dose against another. The posted primary results give estimated mean responses of 0.116 L for placebo, 0.255 L for 1.25 µg, 0.244 L for 2.5 µg, and 0.304 L for 5.0 µg. These estimates describe the trial’s measured responses; they do not, on their own, establish the clinical importance of a difference. A threshold for clinical importance is not reported in the registry record.

3. Trial Design

The registry describes NCT01233284 as a Phase II, randomized, double-blind, placebo-controlled crossover trial. The trial enrolled 149 participants and is listed as completed. The recorded start was 2010-11, and primary completion was 2012-01. Asthma is the listed condition, and Boehringer Ingelheim is the listed sponsor.

Participants received once-daily tiotropium inhalation solution at three dose levels or matching placebo, delivered by Respimat. The crossover model means that treatment comparisons are structured around treatment periods within the trial rather than as a simple parallel comparison of permanently separate groups. In a crossover study, within-participant information can contribute to comparisons because a participant may receive more than one treatment. The registry record does not report the treatment sequence, the length of any washout, or how possible carryover effects were handled.

The main outcome was evaluated at the end of each four-week treatment period. The primary description says that the analysis used a mixed model for repeated measurements, with adjustments for treatment, period, patient, and study baseline. The 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 in a period, further restricted to those with non-missing FEV1 data.

The enrollment count of 149 is not the same as the number contributing to every reported outcome. The primary arm summaries list 144 participants for placebo, 144 for the 1.25 µg dose, 144 for the 2.5 µg dose, and 143 for the 5.0 µg dose. The registry record does not give a complete participant flow or explain all differences between enrollment and the outcome-specific counts.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Randomised, double-blind, placebo controlled, cross-over design without washout phase between the four periods. Patients were randomized to one of the 4 sequences (ABCD, DCBA, BDAC, CADB). For one patient treatment 2 and treatment 3 were interchanged (resulting sequence DBCA).

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:

Period 4 (4 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) reduced to patients with non-missing FEV1 data. The 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.

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 in One Second (FEV1) Peak Within 0-3 Hours Post-dose Response, measured over 10 minutes (min) before drug administration and 30 min, 1h, 2h, 3h after drug administration.

The primary endpoint is the response in forced expiratory volume in one second, or FEV1, measured as the peak within zero to three hours after drug administration. FEV1 is the amount of air a person can forcefully exhale in the first second of a breath. The registry reports the endpoint in litres and defines response as change from baseline at the end of each four-week treatment period.

Measurements for the peak-response assessment were scheduled ten minutes before dosing and at 30 minutes, one hour, two hours, and three hours after dosing. The analysis description says the reported means were adjusted for treatment, period, patient, and study baseline, using a mixed model for repeated measurements. The posted endpoint values are means, with standard errors reported as their dispersion. A standard error describes the precision of an estimated mean; it is not the spread of individual participants’ measurements.

Peak FEV1 within the post-dose window is used to describe lung-function response during the hours after administration. It is one of several measures in the trial, alongside trough FEV1, FEV1 area under the curve, and measures based on forced vital capacity and peak expiratory flow. The endpoint is a physiological measure, not a direct measure of symptoms, daily functioning, or long-term outcomes. Whether a difference in this measure is meaningful to patients is not established by the numerical result alone; a clinical-importance threshold is not reported in the registry record.

7. Results Posted in the Registry

• Tio R1.25 qd: mean 0.26 versus 0.12 on control; difference 0.14 (95% CI 0.06 to 0.21), standardized effect d = 0.43; z-test p = <0.001.
• Tio R2.5 qd: mean 0.24 versus 0.12 on control; difference 0.13 (95% CI 0.05 to 0.20), standardized effect d = 0.40; z-test p = <0.001.
• Tio R5 qd: mean 0.30 versus 0.12 on control; difference 0.19 (95% CI 0.11 to 0.26), standardized effect d = 0.57; 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.

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 qd: mean 0.13 versus 0.01 on control; difference 0.12 (95% CI 0.05 to 0.20), standardized effect d = 0.39; z-test p = 0.001.
  • Tio R2.5 qd: mean 0.14 versus 0.01 on control; difference 0.13 (95% CI 0.06 to 0.21), standardized effect d = 0.41; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Tio R1.25 qd 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 Tio R2.5 qd than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

FEV1 Area Under the Curve 0-3 Hours (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 qd: mean 0.15 versus 0.03 on control; difference 0.13 (95% CI 0.05 to 0.20), standardized effect d = 0.40; z-test p = <0.001.
  • Tio R2.5 qd: mean 0.15 versus 0.03 on control; difference 0.13 (95% CI 0.05 to 0.20), standardized effect d = 0.39; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Tio R1.25 qd 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 Tio R2.5 qd than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Forced Vital Capacity (FVC) Peak Within 0-3 Hours Post-dose 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 qd: mean 0.17 versus 0.09 on control; difference 0.08 (95% CI -0.02 to 0.17), standardized effect d = 0.19; z-test p = 0.100.
  • Tio R2.5 qd: mean 0.16 versus 0.09 on control; difference 0.07 (95% CI -0.02 to 0.17), standardized effect d = 0.17; z-test p = 0.140.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tio R1.25 qd 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 qd and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary lung-function outcomes, including trough FEV1, FEV1 area under the curve, forced vital capacity responses, and peak expiratory flow over time. The posted secondary results span 17 outcomes. The available values show a general pattern in which some FEV1 measures are higher under tiotropium than placebo, and the higher dose has the largest posted mean for some measures. The pattern is not uniform across every outcome or dose, and the observed summaries should not be treated as a single confirmatory finding.

For the posted trough FEV1 and FEV1 area-under-the-curve comparisons, the sponsor reports positive mean differences for the 1.25 µg and 2.5 µg doses compared with placebo. The primary peak FEV1 outcome also has positive sponsor-reported differences for all three doses. Taken together, the posted results are directionally compatible for several FEV1 measures, but not every secondary measure is reported with a sponsor analysis for every dose in the information available. Secondary outcomes provide context for the primary result; they do not replace it.

Multiple outcomes and comparisons create multiplicity: the more statistical tests considered, the more opportunities there are for chance findings. General explanation: when many hypotheses are tested, an isolated small p-value can be less compelling unless the analysis accounts for the testing process or the endpoints were prioritized in advance. The registry record lists 18 outcome measures and 57 analyses, but a multiplicity adjustment or hierarchy for interpreting secondary outcomes is not reported in the registry record.

Accordingly, unadjusted secondary findings carry less weight than a clearly specified primary analysis. They can help describe the breadth and consistency of observed lung-function responses, but their p-values should not be treated as independent confirmation without information about prespecification and multiplicity control. The registry record does not report the complete analysis plan needed to determine which secondary tests were confirmatory and which were exploratory.

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

• Trough FEV1 Response
• FEV1 Area Under the Curve 0-3 Hours (AUC0-3h) Response
• Forced Vital Capacity (FVC) Peak Within 0-3 Hours Post-dose Response
• Trough FVC Response
• FVC AUC0-3h Response
• Individual FEV1 Over Time (at Each Timepoint at Visits) Response
• Individual FVC Over Time (at Each Timepoint at Visits) Response
• Individual Peak Expiratory Flow (PEF) Over Time (at Each Timepoint at Visits) Response

9. Statistical Interpretation

10. Statistical Methods Explained

The primary description identifies a mixed model for repeated measurements, abbreviated MMRM. General explanation: repeated measurements are observations collected at more than one time or under more than one condition. A mixed model can account for the structure of such data, including the fact that measurements from the same participant are related, while estimating treatment comparisons. In this trial, the registry says the means were adjusted for treatment, period, patient, and study baseline. That adjustment is relevant to a crossover design, where treatment periods and participant identity are part of the comparison structure.

What does the mean difference describe?

A mean difference expresses the estimated mean response in one treatment condition relative to another, in the endpoint’s unit. Here the unit is litres, and the comparisons are each tiotropium dose against placebo. For example, the sponsor-reported mean difference for 1.25 µg is 0.138 L. This is a model-based estimate from the registry’s mixed-model analysis. It is not a difference between individual participants’ outcomes, and it does not imply that every participant had the same response.

The posted arm means are adjusted means, according to the primary outcome description. The accompanying standard errors quantify uncertainty in those estimated means. General explanation: a standard error is smaller when an estimate is more precise, all else equal. It should not be read as the range containing most individual participant values. The record does not supply standard deviations for the primary arm means.

Why use a crossover model?

General explanation: a crossover design can use each participant’s experience under multiple treatments, which may make within-participant comparisons informative. Such designs also require attention to treatment sequence, period effects, and possible carryover from one treatment period to another. The registry’s primary description specifies adjustment for period and patient. Details on sequence allocation, washout, and the methods used to assess or address carryover are not reported in the registry record. No assumptions about those aspects can be inferred from the posted estimates alone.

What do the p-values tell the reader?

A p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the analysis. The registry reports p-values < 0.001 for its three primary comparisons. The unadjusted recalculations report p-values <0.001. A small p-value is evidence against a null difference in the context of the model, but it is not the probability that the null hypothesis is true. It also does not measure clinical importance, and it does not describe the probability that the result will repeat in another study.

The sponsor’s reported analyses use mixed models and identify the parameter as mean difference in final values. The primary endpoint description, meanwhile, defines response as change from baseline at the end of each four-week treatment period. The registry does not provide the full statistical analysis plan or enough model output to reconstruct every analytic detail. The sponsor estimates and confidence intervals are therefore best read as the reported model results, while the recalculated estimates are simple, unadjusted comparisons based on posted summaries.

Why can recalculated results differ?

General explanation: analyses using only group-level means and standard errors cannot generally recreate a model that uses participant-level repeated measurements and covariates. A crossover analysis may also use within-participant relationships that are not recoverable from marginal arm summaries. Thus, a recalculated confidence interval or p-value can differ from the registry’s model-based result even when the point estimates are close. The recalculation is a descriptive check, not a substitute for the specified model. In this record, the discrepancy indicator is false, and the sponsor’s reported analyses remain the direct record of the trial’s fitted comparisons.

Finally, statistical significance does not answer every scientific question. The primary comparisons concern the mean FEV1 response against placebo. The record does not report a minimum clinically important difference, a non-inferiority margin, or direct dose-to-dose tests. The model’s result should be kept within that defined scope.

11. Confidence Intervals and Precision

The sponsor-reported 95% confidence intervals describe a range of values compatible with the fitted data and model, under the assumptions used for the analysis. They also show the precision of the estimated mean differences. For the 1.25 µg dose, the mean difference is 0.138 L with a 95% confidence interval from 0.090 L to 0.186 L. For 2.5 µg, it is 0.128 L, with an interval from 0.080 L to 0.176 L. For 5.0 µg, it is 0.188 L, with an interval from 0.140 L to 0.236 L.

All three sponsor-reported intervals lie above zero, consistent with the reported p-values of < 0.001 for each comparison. The intervals do not represent a guarantee that the true difference lies in that particular range. In general, a confidence interval is a measure of uncertainty around an estimate, conditional on the analysis and its assumptions; it does not account for every source of uncertainty, such as unreported design or analysis choices.

The recalculated intervals are not identical to the sponsor’s intervals. The recalculated comparisons use posted summary statistics and are simple, unadjusted estimates; the sponsor reports mixed-model analyses. The registry provides no discrepancy flag, but differences in methods mean that the sponsor-reported model estimates and intervals should be interpreted as the trial’s principal fitted results. The close point estimates do not make the intervals interchangeable.

Precision is also distinct from clinical importance. An interval can be relatively narrow while still leaving uncertainty about whether its range corresponds to a meaningful change for patients. No clinical-importance threshold is reported in the registry record. The confidence intervals concern the estimated average response, not the range of individual treatment responses, and the posted results do not quantify how much participants varied from one another.

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 figures are planning illustrations based on the observed effect in this trial, not a reconstruction of the trial’s original design calculations. The assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect targeted for detection is set to the stated fraction of the observed effect. These continuous-outcome figures are participants per arm, not total events.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the target effect under those assumptions, if the effect and other assumptions are correct. The 90% power column describes the corresponding planning target for a 90% chance. These are design-planning probabilities, not guarantees for a future study. They are also not observed power: observed power is not a useful substitute for interpreting the estimate and its uncertainty after the trial has been conducted.

The rows for 100%, 75%, and 50% of the observed effect illustrate progressively smaller effects as planning targets. Smaller effects generally require more participants to detect with the same planned power, all else equal. This is why the participant counts increase as the assumed effect is reduced. The counts are scenario-specific illustrations, not a recommendation for a new trial. The registry record does not report the original sample-size justification or the assumptions used to choose the enrollment target of 149.

Because this trial used a crossover design and the illustration assumes equal allocation between two arms, these figures should not be treated as a design simulation for the original multi-period study. They do not incorporate every feature of a crossover analysis, such as within-participant correlation or treatment sequence. They only convey how planning counts respond to alternative assumed effect sizes under the stated simplified assumptions.

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 = 0.139; pooled standard deviation σ = 0.324.
2. n = 2 × (1.96 + 0.842)² × 0.324² / 0.139² = 85.3, rounded up to 86 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 <- 0.139                      # observed difference in means
sigma <- 0.324                     # 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(1233284)
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 = 86 (80% power), 115 (90% power)
 75% of observed effect: n per arm = 152 (80% power), 203 (90% power)
 50% of observed effect: n per arm = 342 (80% power), 457 (90% power)
power.t.test: 86.3 
Simulated power at n = 86 per arm: 0.803 (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 registry reports the sponsor’s primary comparisons from a mixed-model analysis. The mean differences are 0.138 L for 1.25 µg, 0.128 L for 2.5 µg, and 0.188 L for 5.0 µg, each compared with placebo. Their 95% confidence intervals are 0.090 to 0.186 L, 0.080 to 0.176 L, and 0.140 to 0.236 L, respectively. Each reported p-value is < 0.001.

The unadjusted recalculations from the posted summary statistics are 0.139 L, 0.128 L, and 0.188 L, with p-values <0.001. These simple calculations are useful as a numerical cross-check, but they are not the same analysis as the sponsor’s model. The trial description specifies adjustment for treatment, period, patient, and baseline, and the crossover measurements contain within-participant structure that summary-level recalculation cannot fully represent.

The registry does not flag a discrepancy between the recalculations and the sponsor analyses. The sponsor’s mixed-model estimates are the reported trial analyses; the recalculations are supplementary, unadjusted estimates. The full statistical analysis plan and detailed model output are not reported in the registry record, so the precise reasons for small differences in estimates or intervals cannot be established from the posted information alone.

15. Multiplicity, Missing Data and Analysis Populations

The record reports a primary FEV1 endpoint alongside numerous other outcome measures and analyses. It lists 18 outcome measures, 17 posted secondary outcomes, and 57 analyses. With multiple outcomes, time points, and dose comparisons, the chance of at least one apparently notable result can increase if tests are interpreted without adjustment. General explanation: multiplicity procedures can control or otherwise organize this risk, for example by defining a testing hierarchy or adjusting significance thresholds. Whether such a procedure was used is not reported in the registry record.

The primary analysis population is described as the full analysis set, defined as randomized and treated participants with baseline data and at least one on-treatment efficacy measurement after four weeks on treatment within a period, then reduced to participants with non-missing FEV1 data. This definition makes clear that the primary analysis is not necessarily based on every randomized participant. The registry lists 149 enrolled participants, while the primary summaries show outcome-specific counts of 144, 144, 144, and 143 across the four treatment conditions.

The record does not provide a full account of missing measurements, reasons for missingness, participant discontinuations, or the handling of incomplete records in the model. MMRM is named for the primary analysis, but details such as its missing-data assumptions, covariance structure, and sensitivity analyses are not reported in the registry record. These omissions limit an independent assessment of how incomplete data may have affected the estimates.

The trial’s original sample-size justification, any interim analyses, and the complete statistical analysis plan are not reported in the registry record. It is therefore not possible to establish from the posted information whether the enrollment target was based on a particular effect size, how the primary and secondary hypotheses were prioritized, or whether planned safeguards against selective interpretation were used. The sample-size illustrations are separate planning exercises and should not be mistaken for the trial’s original design rationale.

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: inguinal hernia (0.7%), alcohol abuse (0.7%), panic attack (0.7%).

The registry’s serious adverse event figures list zero affected participants for placebo, zero for the 1.25 µg dose, zero for the 2.5 µg dose, and two for the 5.0 µg dose. The corresponding numbers at risk are 144, 146, 147, and 146. These are counts in the posted safety record; the denominators differ from some primary efficacy counts, as expected from the separately listed safety groups and analysis populations.

The record lists inguinal hernia, alcohol abuse, and panic attack as serious adverse event terms, each at 0.7%. It does not establish in the information available whether each term was considered related to treatment, and the listed terms should not be interpreted as proof of causation. The number of deaths is not reported in the registry record.

These figures describe serious adverse events as recorded; they do not provide a complete basis for comparing overall safety. The registry’s posted figures show zero other adverse events affected in each listed group, but the record’s event counts do not alone establish the absence of other harms. The trial’s size and duration, as well as the limited details available about safety-event collection and attribution, constrain what can be concluded from these counts.

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

The primary results describe estimated changes in peak FEV1 within three hours after dosing, at the end of each four-week treatment period. The registry’s fitted comparisons show higher mean responses for each tiotropium dose than for placebo, with positive reported mean differences and 95% confidence intervals above zero. The results therefore provide evidence of differences in this particular lung-function outcome under the trial’s analysis.

That statistical finding does not establish how important the differences are to patients. A clinically meaningful threshold is not reported in the registry record, and the endpoint is not itself a direct measure of symptoms, daily functioning, or long-term asthma outcomes. The posted primary estimates also do not demonstrate that one dose is better than another: the analyses compare each dose with placebo, and direct dose-to-dose comparisons are not reported.

The trial evaluates treatment over four-week periods in people with moderate persistent asthma who remained symptomatic despite regular inhaled corticosteroid maintenance therapy. The registry does not report results that establish effects beyond the measured treatment periods, nor does the primary result address all aspects of efficacy or safety. The posted secondary outcomes add information about other lung-function measures, but multiplicity and incomplete analysis-plan details warrant caution in treating those findings as definitive.

Finally, this is a Phase II study with 149 enrolled participants and fewer participants in the primary outcome summaries. The data describe what was observed and estimated in this trial population. They do not guarantee that the same estimates will be seen in another study or a different population, and they do not replace clinical judgment or constitute medical advice.

18. Why This Trial Matters Statistically

This trial illustrates how the analysis needs to reflect the design. In a crossover study, participants contribute information across treatment periods, and treatment, period, and participant terms matter to the comparison. The registry identifies a mixed model for repeated measurements and says that its estimates are adjusted for treatment, period, patient, and baseline. This is an important distinction from treating each dose group as if it were an unrelated parallel arm.

It also demonstrates why two sets of estimates can be close without representing the same calculation. The sponsor’s mixed-model results and the unadjusted recalculations from posted summaries are numerically similar, but the model incorporates design and participant-level structure that summary statistics cannot fully reproduce. Reporting both the fitted analysis and a transparent recalculation helps readers understand the role of analytic assumptions without confusing the two.

The record also highlights the distinction between statistical evidence and clinical importance. The primary intervals exclude zero, yet the registry does not report a threshold for a meaningful FEV1 change. A small p-value and a positive mean difference address evidence for an average difference under the model; they do not determine whether that difference matters to patients.

Finally, secondary measures and safety counts add context but require disciplined interpretation. Many outcomes and analyses are listed, while multiplicity methods and a complete analysis plan are not reported. The serious adverse event counts are small and descriptive, rather than a complete basis for comparing safety. Together, these features make the study a useful example of why design-aware models, uncertainty intervals, endpoint scope, and registry reporting gaps all matter when interpreting clinical-trial results.

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 registry record does not report the treatment sequence, washout details, or the approach to possible carryover effects in this crossover trial. Although the primary model adjusts for period and patient, the available description does not permit an independent review of the full model specification or of how the design features were handled in detail.

The registry does not report a complete participant flow, reasons for missing data, detailed missing-data assumptions, or sensitivity analyses. The primary analysis is restricted to participants with non-missing FEV1 data and at least one on-treatment efficacy measurement after four weeks in a period. Differences between the enrollment count and outcome-specific analysis counts therefore cannot be fully explained from the posted record.

The complete statistical analysis plan, original sample-size justification, interim analyses, and multiplicity procedures are not reported in the registry record. This limits assessment of whether outcome and comparison priorities were set in advance and how secondary findings should be weighted. The reported trial analyses and the simple unadjusted recalculations also answer related but not identical statistical questions.

The primary endpoint concerns a short-term physiological measure. The record does not report a threshold for clinical importance, and the primary result does not by itself establish effects on symptoms, longer-term asthma control, or other patient-centered outcomes. Safety interpretation is also constrained: only serious adverse event counts are detailed in the listed figures, deaths are not reported, and treatment relatedness is not established for the listed event terms. These limitations call for a narrow reading of the results rather than extrapolation beyond the measured outcomes and period.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Randomised, Double- Blind, Cross-over Efficacy and Safety Comparison of Three Different Doses of Tiotropium Administered Once Daily Versus Placebo in Patients With Moderate Persistent Asthma. — NCT01233284.
• Registry record last updated 2013-12-24; status last verified 2013-09.
• Results first posted 2013-01-21.
• 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

NCT01233284 is a completed Phase II randomized, double-blind, placebo-controlled crossover trial of once-daily tiotropium inhalation solution delivered by Respimat in people with moderate persistent asthma. It enrolled 149 participants and compared doses of 1.25 µg, 2.5 µg, and 5.0 µg with matching placebo.

The primary endpoint was change from baseline in peak FEV1 within zero to three hours after dosing, measured at the end of each four-week treatment period. The registry reports positive mixed-model mean differences versus placebo for all three doses, with 95% confidence intervals above zero. Results should be interpreted as estimates of this specific lung-function outcome, with uncertainty and reporting limitations in mind. The registry record does not report the complete analysis plan, multiplicity handling, original sample-size justification, or clinical-importance threshold.