Efficacy and Safety of 2 Doses of Tiotropium Respimat® Compared to Placebo in Children With Moderate Persistent Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of 2 Doses of Tiotropium Respimat® Compared to Placebo in Children With Moderate Persistent Asthma (NCT01634139), a randomized phase 3 study. The primary outcome is FEV1 Peak (0-3h) Change From Baseline.

2. Clinical Question

The clinical question concerns a continuous lung-function measure: peak FEV1, expressed in litres, during the 0-to-3-hour period after dosing. The primary outcome is a change from baseline, rather than a single lung-function reading at week 24. A positive change describes an increase relative to baseline; the trial estimates how the mean change differed across randomized groups.

The endpoint is one component of a broader evaluation. The registry lists additional lung-function outcomes, including FEV1 and FVC measures at week 48 and area-under-the-curve measures. Safety was also evaluated, although the posted adverse-event information is limited to counts and selected serious-event terms. These outcomes help describe what was measured, but they do not replace the prespecified primary comparison.

3. Trial Design

This was a Phase 3, randomized, double-blind, parallel-group trial sponsored by Boehringer Ingelheim. It enrolled 403 participants and compared tiotropium at two doses with placebo in children aged 6 to 11 years with moderate persistent asthma. The registry lists the trial as completed. The recorded start was 2012-07, and primary completion was 2015-06.

The three groups were placebo Respimat, tiotropium Respimat 2.5 mcg, and tiotropium Respimat 5 mcg. The official title describes once-daily evening dosing over 48 weeks. Random allocation supports a comparison between assigned groups, while double masking is intended to reduce the influence of treatment knowledge on participants’ experiences and outcome assessment. The registry identifies the trial as parallel-group, meaning participants were assigned to a group rather than crossing between treatments.

The primary endpoint was measured at week 24. Its posted analysis included 126 participants in the placebo group, 131 in the 2.5 mcg group, and 134 in the 5 mcg group. Those counts are the numbers with available outcome data at the timepoint, according to the registry description; they should not be confused with the total enrollment or interpreted as the number originally randomized to each group.

The Full Analysis Set was defined as the treated set: randomized participants who received at least one documented dose of study medication. The registry says that missing data at a visit were imputed using available data from that participant at that visit, and completely missing data were handled by the statistical model. Further details about the original sample-size justification, allocation procedures, or the full statistical analysis plan are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) was equal to treated set which included all randomised patients who received at least 1 documented dose of study medication. Missing data at a visit was imputed by available data from the patient at that visit. Completely missing data were handled by the statistical model.

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.

Population: Treated Set (TS): This patient set included all randomised patients who were dispensed study medication and were documented to have taken at least 1 dose of investigational treatment.

6. Primary Endpoint

The registry lists the primary outcome as FEV1 Peak (0-3h) Change From Baseline, measured over Baseline and 24 Weeks..

The primary endpoint is change from baseline in peak forced expiratory volume in 1 second, or FEV1, during the first 3 hours after dosing, measured at week 24. FEV1 is the volume of air exhaled in the first second of a forced breath; the registry reports the outcome in litres. Peak FEV1 in the post-dose window summarizes the highest measured lung-function response within that interval, rather than relying on one isolated measurement.

Expressing the outcome as change from baseline focuses the comparison on how each group’s measurement shifted from its own starting value. The posted group means are described as adjusted means, and the registry identifies standard errors as the measure of dispersion. The analysis population includes participants who were randomized and received at least one documented dose, with the number analyzed reflecting participants with available data at the timepoint.

FEV1 is used as a continuous physiological outcome, so the treatment contrast is expressed as a difference in mean change between a tiotropium group and placebo. The measure captures a lung-function dimension that can be compared quantitatively across groups. It does not by itself describe symptoms, daily functioning, exacerbations, or the full safety profile. Those are distinct clinical considerations, and the posted primary endpoint should be interpreted as evidence about this specified lung-function measure at week 24.

In general, a mean difference describes the average contrast between groups, while uncertainty around that estimate is represented by a confidence interval. Neither the endpoint nor a group average alone gives the experience of every individual participant.

7. Results Posted in the Registry

• Tio R2.5: mean 0.40 versus 0.23 on control; difference 0.17 (95% CI 0.10 to 0.24), standardized effect d = 0.57; z-test p = <0.001.
• Tio R5: mean 0.39 versus 0.23 on control; difference 0.16 (95% CI 0.09 to 0.24), standardized effect d = 0.54; 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.

FEV1 Peak (0-3h) at Week 48 Change From Baseline

• 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 R2.5: mean 0.47 versus 0.35 on control; difference 0.12 (95% CI 0.05 to 0.20), standardized effect d = 0.41; z-test p = 0.001.
  • Tio R5: mean 0.48 versus 0.35 on control; difference 0.13 (95% CI 0.05 to 0.20), standardized effect d = 0.42; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Tio R2.5 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 R5 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

FEV1 AUC (0-3h) Change From Baseline

• 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 R2.5: mean 0.31 versus 0.15 on control; difference 0.15 (95% CI 0.08 to 0.22), standardized effect d = 0.53; z-test p = <0.001.
  • Tio R5: mean 0.31 versus 0.15 on control; difference 0.16 (95% CI 0.09 to 0.23), standardized effect d = 0.54; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Tio R2.5 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 R5 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

FVC AUC (0-3h) Change From Baseline

• 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 R2.5: mean 0.23 versus 0.13 on control; difference 0.10 (95% CI 0.02 to 0.19), standardized effect d = 0.31; z-test p = 0.012.
  • Tio R5: mean 0.21 versus 0.13 on control; difference 0.08 (95% CI -0.00 to 0.16), standardized effect d = 0.23; z-test p = 0.065.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Tio R2.5 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tio R5 and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary lung-function outcomes generally follow a pattern in which the tiotropium groups have higher mean changes than placebo. This includes additional FEV1 measures and FVC measures, assessed at other timepoints or across post-dose measurement windows. The pattern is broadly consistent with the direction of the primary week-24 peak FEV1 comparison, but secondary outcomes are not interchangeable with the primary endpoint: they measure different aspects of lung function or are evaluated at different times.

The registry lists 30 posted secondary outcomes, while the trial record reports many outcome measures and analyses overall. A large set of comparisons creates more opportunities for nominally small p-values to occur by chance. Unless a suitable multiplicity strategy was prespecified and applied, individual secondary p-values should carry less inferential weight than the primary result. Whether such an adjustment was used is not reported in the registry record.

Secondary estimates can still be useful for describing whether findings are directionally consistent across related measures and for identifying questions that may warrant further study. However, the pattern does not independently confirm the primary result, and it should not be treated as proof that every secondary outcome differed reliably from placebo. The analyses may also differ in the amount of available data at each timepoint.

The week-48 peak FEV1 measure extends observation beyond the primary week-24 endpoint, while FEV1 and FVC area-under-the-curve measures summarize measurements across a post-dose interval. These distinctions matter for interpretation: one outcome represents a peak reading, another an average over an interval, and another a different lung-function quantity. The secondary findings should therefore be understood as supporting context rather than a substitute for the primary comparison or a complete account of clinical benefit and risk.

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

• Trough FEV1 Change From Baseline
• FEV1 Peak (0-3h) at Week 48 Change From Baseline
• FEV1 AUC (0-3h) Change From Baseline
• FEV1 Change From Baseline at Each Individual Timepoint
• FVC Peak(0-3h) Change From Baseline
• Trough FVC Change From Baseline
• FVC AUC (0-3h) Change From Baseline
• FVC Change From Baseline at Each Individual Timepoint

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a mean change in FEV1 measured in litres. The reported analysis compares the adjusted mean change in each tiotropium group with the adjusted mean change in placebo. This is a natural way to summarize a continuous outcome, but the mean difference is a group-level quantity. It does not imply that every participant experienced a change equal to the group average.

What does the mean difference represent?

For tiotropium 2.5 mcg, the registry’s mixed-model estimate of the net mean difference versus placebo was 0.170 litres. For 5 mcg, the estimate was 0.164 litres. A positive contrast means the estimated average change was higher in the active-treatment group than in the placebo group. The contrasts are reported alongside 95% confidence intervals and p-values. The method used for these reported comparisons is identified as Mixed Models Analysis.

In general, a mixed model can analyze outcome information across visits and account for the relationship among repeated measurements from the same participant. The registry describes missing-data handling at visits and for completely missing data, but does not report model details such as its exact structure, covariance assumptions, or all included terms. Those details should not be inferred from the method label alone.

How should the p-values be read?

In general, a p-value describes how compatible the observed data are with a specified null hypothesis, under the analysis assumptions. The reported primary p-values are each < 0.001. They are not the probability that the null hypothesis is true, and they do not measure the clinical importance of the estimated difference. The registry labels the analyses as superiority or other, but the available record does not provide a complete account of the hypothesis-testing plan or any multiplicity adjustment.

The recalculated comparisons use simple, unadjusted calculations from the posted group summaries. Their estimates are 0.17 litres and 0.164 litres, and both recalculated p-values are <0.001. The recalculation does not reproduce the sponsor’s full mixed-model analysis. It does not use participant-level data, and it cannot account for model features that are not represented by the posted summary statistics. It is therefore a check on the broad numerical pattern rather than a replacement for the reported analysis.

What do standard errors describe?

The registry gives standard errors beside the adjusted group means. In general, a standard error describes the estimated sampling variability of a statistic, such as a mean; it is not the spread of individual participants’ measurements. Standard errors can help convey how precisely a mean has been estimated, but interpretation of the treatment contrast is better informed by the confidence interval for that contrast. The registry does not provide standard deviations for the adjusted means in the posted primary outcome.

The Full Analysis Set was the treated set, comprising randomized participants who received at least one documented dose. For the primary timepoint, the analyzed counts were 126 for placebo, 131 for tiotropium 2.5 mcg, and 134 for tiotropium 5 mcg. The outcome description says the analyzed count represents participants with available data at the timepoint. It also states that missing data at a visit were imputed from available data for that participant at that visit, while completely missing data were handled by the statistical model. The detailed imputation rules and the model’s assumptions for completely missing outcomes are not reported in the registry record.

In general, inferences from a model that handles missing outcomes depend on assumptions about how missingness relates to observed and unobserved outcomes. The registry’s concise description does not establish whether those assumptions were tested or whether sensitivity analyses were conducted. Nor does it identify the number or reasons for missing measurements at each visit.

Why is multiplicity relevant?

The record lists many outcomes and analyses, including multiple lung-function measures and timepoints. In general, when numerous statistical tests are conducted, the chance of at least one nominally unusual result can increase. A prespecified multiplicity strategy can address this issue, but the strategy is not reported in the registry record. The primary endpoint remains the main result to emphasize, while secondary p-values should be read more cautiously.

The sample-size illustrations are also distinct from the trial’s original design calculations. In general, power is the probability that a study will detect an effect of a specified size under specified assumptions if that effect is present. The illustrations use the observed effect and stated planning assumptions; they are not the trial’s original sample-size justification. The original design assumptions are not reported in the registry record.

11. Confidence Intervals and Precision

A confidence interval describes a range of values compatible with the data and analysis assumptions at a stated confidence level. It expresses uncertainty around an estimated contrast; it is not a range containing a specified proportion of individual participants’ responses. A narrower interval indicates greater precision, while a wider interval indicates more uncertainty about the size of the mean difference.

For the primary comparison of tiotropium 2.5 mcg with placebo, the reported mean difference was 0.170 litres, with a 95% confidence interval from 0.108 to 0.231. For the 5 mcg comparison, the reported mean difference was 0.164 litres, with a 95% confidence interval from 0.103 to 0.255. Both intervals lie above zero. Their widths also show that the point estimates should not be read as exact values: the data remain compatible with a range of possible mean differences under the reported model.

Precision is not the same as clinical importance. The confidence intervals quantify uncertainty in the estimated group contrast, but the registry record does not give a threshold for judging whether a difference in litres is meaningful to children or families. A statistically precise estimate can still require clinical context, and a confidence interval does not address all sources of uncertainty, such as missing-data assumptions or the selection of outcomes for emphasis.

The reported intervals come from the sponsor’s mixed-model analysis. The simple recalculation from posted summary statistics uses a different, unadjusted approach and produces different interval limits. Those recalculated limits are not a reason to replace the sponsor’s own intervals; the reported analysis takes precedence for interpretation. The registry does not provide participant-level data or enough model detail to independently reproduce its confidence intervals.

For the primary outcome, the intervals support a positive estimated average contrast relative to placebo under the reported analysis. They do not show the degree of response for any particular participant, establish a difference between active doses, or resolve how the result relates to other clinical outcomes.

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 planning figures describe hypothetical sample sizes for future two-group studies based on the observed mean difference and the stated planning assumptions. For these continuous outcomes, the figures are participants per arm, not total events. They are not the numbers enrolled in this trial and should not be confused with the analyzed participant counts.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect: the full observed effect, 75% of it, or 50% of it. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect is present. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are design calculations, not observed outcomes. They do not say whether the completed trial had a particular probability of finding a result after the data were collected.

The rows planning for smaller effects require more participants per arm than rows planning for the full observed effect. This is expected in general: a smaller group difference is harder to distinguish from sampling variation, so more information is needed to detect it with the same planned power. Figures are illustrations rather than recommendations, and their relevance depends on whether the planning assumptions and target effect are suitable for the intended future study. This is not observed power.

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 = 0.170; pooled standard deviation σ = 0.300.
2. n = 2 × (1.96 + 0.842)² × 0.300² / 0.170² = 49.0, rounded up to 49 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 <- 0.17                      # observed difference in means
sigma <- 0.300287639883274                     # 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(1634139)
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 = 49 (80% power), 66 (90% power)
 75% of observed effect: n per arm = 88 (80% power), 117 (90% power)
 50% of observed effect: n per arm = 196 (80% power), 263 (90% power)
power.t.test: 50 
Simulated power at n = 49 per arm: 0.789 (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’s own primary analysis used Mixed Models Analysis and reported a mean difference of 0.170 litres for tiotropium 2.5 mcg versus placebo, with a 95% confidence interval from 0.108 to 0.231 and p < 0.001. For tiotropium 5 mcg versus placebo, it reported a mean difference of 0.164 litres, with a 95% confidence interval from 0.103 to 0.255 and p < 0.001.

The simple recalculations from posted summary statistics give mean differences of 0.17 and 0.164 litres, with p-values of <0.001 for both. These are unadjusted comparisons and do not reproduce the mixed-model analysis. Their role is to provide a rough check using the posted group summaries, not to serve as the primary inferential result.

The registry record does not flag a discrepancy. The sponsor’s own analysis therefore takes precedence. The two approaches yield a similar overall pattern, but the sponsor’s model-based confidence intervals and p-values should be used when describing the trial’s reported primary inference. The record does not provide sufficient detail or participant-level data to reconstruct that analysis independently.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports a substantial collection of outcomes and analyses, including multiple lung-function measures and assessment times. When many hypotheses are tested, nominal p-values can overstate the strength of evidence if the testing plan does not account for multiplicity. A statistical plan may specify a hierarchy, adjustment procedure, or other approach for controlling interpretation across tests. Whether such a procedure was used for the primary and secondary analyses is not reported in the registry record.

This gap matters most when interpreting secondary results. The primary endpoint is clearly identified, so it should remain the main focus. Secondary comparisons can show whether estimates point in a similar direction, but a collection of unadjusted tests does not provide the same confirmatory evidence as a prespecified, multiplicity-controlled analysis. The record does not report a complete hierarchy of hypotheses or clarify how the many reported analyses were prioritized.

The registry describes the analysis population as the Full Analysis Set, equal to the treated set, including all randomized participants who received at least one documented dose. For each timepoint, the number analyzed is described as the number with available data. Missing data at a visit were imputed using that participant’s available data at the visit, while completely missing data were handled by the statistical model.

The record does not report detailed counts or reasons for missing outcome data, the exact imputation procedure, or the assumptions used by the statistical model for completely missing data. It also does not report sensitivity analyses assessing whether alternative missing-data assumptions would change the estimates. In general, missing-data methods rely on assumptions about the relationship between observed and unobserved outcomes; the brief registry description is not sufficient to evaluate those assumptions fully.

The stated analysis population does not establish that every randomized participant contributed to every outcome analysis. It identifies the broad population definition, while the timepoint-specific analyzed counts reflect data availability. A complete assessment of potential bias would require additional information about follow-up, missingness, the model specification, and the planned analysis procedures, which are not reported in the registry record.

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

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: asthma (1.5%), anaphylactic reaction (0.8%), gastroenteritis (0.8%), renal abscess (0.8%), concussion (0.8%).

The posted safety counts distinguish serious adverse events from other adverse events. For serious adverse events, the registry reports 6 affected participants among 131 at risk in the placebo group, 3 among 135 in the tiotropium 2.5 mcg group, and 1 among 135 in the tiotropium 5 mcg group. These are participant counts, not event rates calculated here, and they do not show the timing, duration, or clinical course of each event.

Selected serious-event terms listed in the record include asthma at 1.5%, and anaphylactic reaction, gastroenteritis, renal abscess, concussion, and fall at 0.8% each. The registry also reports other adverse events in 79 of 131 placebo participants, 76 of 135 participants receiving 2.5 mcg, and 71 of 135 receiving 5 mcg. These broad counts do not describe severity, recurrence, or whether an event was judged related to study treatment.

Deaths are not reported in the registry record. The counts should be interpreted as descriptive safety information, not as a complete assessment of comparative risk. The posted figures alone do not establish that one group was safer, and they do not capture the full context needed to interpret individual events.

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

The primary result describes an average difference in change from baseline in peak FEV1 at week 24 between each tiotropium group and placebo. The sponsor’s mixed-model estimates were 0.170 litres for 2.5 mcg and 0.164 litres for 5 mcg, with both reported 95% confidence intervals above zero and p < 0.001. This is evidence about the specified continuous lung-function endpoint under the reported analysis.

It does not establish that every child had an increase in FEV1, that every child experienced the same change, or that the measured difference translated into a particular symptom or daily-life outcome. The registry does not report a threshold for clinical importance on this endpoint. The result also does not directly compare the two active doses, since the reported primary analyses compare each dose with placebo.

The trial’s broader context includes other lung-function outcomes and safety counts. Secondary results can provide context, but their interpretation is limited by the number of outcomes and analyses and by the absence of a reported multiplicity approach. Safety counts are descriptive and do not alone establish comparative risk. Neither the primary endpoint nor these summaries provide a complete account of benefits and harms for an individual child.

In general, a randomized, double-blind comparison helps reduce some sources of bias in treatment comparisons, but it does not remove uncertainty about outcome measurement, missing data, model assumptions, or the relevance of an endpoint to patients. Further details about the analysis plan, missingness, and clinical interpretation are not reported in the registry record. The appropriate conclusion is therefore limited to the posted group-level estimates and their uncertainty, rather than a broad claim about treatment effects beyond the measured outcomes.

18. Why This Trial Matters Statistically

Statistically, this trial is useful because it reports a randomized comparison of two active doses against placebo and identifies a continuous primary endpoint with a defined measurement window and follow-up time. Its double-blind, parallel-group design provides a clear framework for interpreting group-level contrasts, while the adjusted means, confidence intervals, and p-values allow readers to distinguish the estimated magnitude from its statistical uncertainty.

The two primary estimates are similar in magnitude, and both sponsor-reported confidence intervals lie above zero. That makes the primary result straightforward to describe as a positive estimated average contrast on the week-24 peak FEV1 measure. At the same time, the record does not report a direct active-dose comparison, so the similar placebo contrasts should not be used to claim equivalence between doses.

The registry also illustrates why statistical significance and clinical meaning are different questions. A small p-value does not quantify the importance of the change, and the record gives no threshold for interpreting the size in clinical terms. Secondary outcomes and safety counts add context but bring their own limitations, including multiple comparisons and limited detail.

Finally, the registry makes explicit some important analysis features, such as the treated-set definition and the broad handling of missing data, while leaving other details unreported. This helps readers identify both what the posted analysis supports and what cannot be evaluated from the record alone. Sample-size illustrations based on observed effects can aid future planning, but they should not be mistaken for the original trial’s design rationale or for evidence about the completed trial’s power.

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 provides a concise account rather than a complete protocol or statistical analysis plan. It does not report the original sample-size justification, detailed allocation procedures, model specification, or a complete account of hypothesis testing. The absence of those details limits independent assessment of whether every analysis followed a prespecified plan.

The primary endpoint is a physiological measure at week 24. The record does not give a threshold for clinical importance or connect the mean change to symptoms, function, or other outcomes meaningful to children and families. Group means also conceal variation in individual response. The posted analyses do not establish how many participants experienced particular levels of change.

Missing-data handling is described only in broad terms. The record does not provide timepoint-specific missing-data counts and reasons, the detailed imputation procedure, model assumptions for completely missing measurements, or sensitivity analyses. Those omissions make it difficult to assess how robust the estimates are to missingness.

Multiple secondary outcomes and analyses are reported, but a multiplicity strategy is not reported in the registry record. As a result, secondary p-values should not be treated as independently confirmatory without further information. The record also provides limited safety detail: serious-event counts and selected terms are available, but information about event timing, duration, severity, treatment relationship, and follow-up is not reported in the registry record. Deaths are not reported in the registry record.

Finally, the trial enrolled children aged 6 to 11 years with moderate persistent asthma. The record does not establish that findings apply to other ages or populations. These limits concern the scope of inference from the registry information and do not change the numerical estimates reported for the studied endpoint.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of 2 Doses of Tiotropium Respimat® Compared to Placebo in Children With Moderate Persistent Asthma — NCT01634139.
• Registry record last updated 2016-07-12; status last verified 2016-06.
• Results first posted 2016-07-12.
• 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

NCT01634139 was a completed Phase 3 randomized, double-blind, parallel-group trial sponsored by Boehringer Ingelheim. It enrolled 403 children aged 6 to 11 years with moderate persistent asthma and compared once-daily evening tiotropium Respimat at 2.5 mcg and 5 mcg with placebo over 48 weeks.

The primary outcome was change from baseline in peak FEV1 during the first 3 hours after dosing at week 24. The sponsor’s mixed-model analyses reported mean differences versus placebo of 0.170 litres for 2.5 mcg and 0.164 litres for 5 mcg; both reported p-values were < 0.001.

The record also lists secondary lung-function outcomes and adverse-event counts. Multiplicity procedures, detailed model specifications, the original sample-size justification, and fuller missing-data sensitivity analyses are not reported in the registry record.