Tiotropium Bromide in Cystic Fibrosis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Tiotropium Bromide in Cystic Fibrosis (NCT01179347), a randomized phase 3 study. The primary outcome is Forced Expiratory Volume in 1 Second (FEV1) Area Under the Curve 0-4 Hours (AUC0-4h) Response.

2. Clinical Question

3. Trial Design

The registry record describes a phase 3, randomized, double-blind, placebo-controlled, parallel-group trial of tiotropium in cystic fibrosis. The study title identifies tiotropium bromide, and the official title specifies a 12-week assessment of tiotropium 5 mcg administered once daily through the Respimat® device. Both active treatment and placebo are described as two inhalations once daily.

The registry lists enrollment as 464. The primary endpoint analysis reports 146 participants in the placebo group and 292 in the tiotropium group. Those endpoint counts should not be treated as the complete randomized-group counts: the adverse-event record gives different at-risk counts, and the primary analysis population has its own eligibility definition. The registry record does not report the original allocation ratio or a detailed account of participant flow.

The study began in 2010-09 and had primary completion in 2012-03. Its status is completed. The primary outcome was FEV1 AUC0-4h response after 12 weeks, with pulmonary-function measurements taken before dosing and at specified post-dose times. Secondary outcomes included FVC measures, pre-bronchodilator FEF25-75, pulmonary exacerbations, and the revised Cystic Fibrosis Questionnaire score. The registry record lists seven outcome measures and six analyses, while five secondary outcomes are posted in the record.

The record says the Full Analysis Set comprised treated patients with at least one baseline and at least one post-baseline on-treatment pulmonary function measurement. The analysis population was further reduced to patients with observed wash-out compliance. The registry record does not report the original sample-size justification or the detailed allocation procedures.

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: First part: double-blind, duration was 12 weeks, 464 patients were randomised to either Tio R5 or placebo in a 2:1 ratio, but 1 randomised patient was not treated. Second part: open-label, all patients received the active treatment for a minimum of 12 weeks to enlarge the safety database.

Double-blind Period (12 Weeks)

Reasons for not completing this period:

Open-label Period (12 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) with imputation reduced to patients with observed wash-out compliance. The FAS was defined as all patients in the treated set who had at least 1 baseline pulmonary function test (PFT) measurement and at least 1 post-baseline on-treatment PFT measurement. No patients \<5 years of age were included in the FAS.

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 1 Second (FEV1) Area Under the Curve 0-4 Hours (AUC0-4h) Response, measured over 30 minutes (min) before first dosing of study drug (defined as baseline), at 1 hour (h), 2 h , 3 h, and 4 h post dosing at day 1 and at 30 min before dosing, at 1 hour, 2 h , 3 h, and 4 h post dosing after 12 weeks..

The primary endpoint is the change from baseline in FEV1 AUC0-4h after the 12-week double-blind treatment period, expressed as percent of predicted. FEV1 is the volume of air expelled in the first second of a forced exhalation. AUC0-4h combines measurements across the period after dosing, rather than relying on a single post-dose reading. In this trial, the area was normalized for time and calculated using the trapezoidal rule divided by the observation time of 4 hours.

The registry specifies measurements at baseline and at 1, 2, 3, and 4 hours after dosing, including assessments on day 1 and after 12 weeks. The endpoint is intended to capture the average pulmonary-function response across the post-dose observation period. Expressing the result as percent of predicted places the measure on a scale referenced to predicted lung function, while the change-from-baseline definition focuses the comparison on change over treatment rather than only the final measurement.

As a continuous endpoint, the group result is reported as an adjusted mean, with standard error describing the uncertainty of that mean. The between-group estimate is a mean difference. A positive estimate indicates a higher mean change in the tiotropium group than in the placebo group on this scale; it does not by itself establish how precise the estimate is or whether the data exclude no difference. Those questions depend on the confidence interval and the model-based analysis.

7. Results Posted in the Registry

• Tio R5 qd: mean 2.51 versus 0.87 on control; difference 1.64 (95% CI -0.29 to 3.57), standardized effect d = 0.17; z-test p = 0.095.

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.

Forced Vital Capacity (FVC) Area Under the Curve 0-4 Hours (AUC0-4h) 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 R5 qd: mean 1.27 versus 0.17 on control; difference 1.10 (95% CI -0.70 to 2.90), standardized effect d = 0.12; z-test p = 0.231.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tio R5 qd and the control. The interval gives the range of effects that remain compatible with the data.

Trough FVC 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 R5 qd: mean 1.51 versus 0.30 on control; difference 1.21 (95% CI -0.64 to 3.06), standardized effect d = 0.13; z-test p = 0.201.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tio R5 qd and the control. The interval gives the range of effects that remain compatible with the data.

Pre-bronchodilator Forced Expiratory Flow Between 25 Percent and 75 Percent of the FVC (FEF25-75) 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 R5 qd: mean 3.02 versus 2.15 on control; difference 0.87 (95% CI -2.69 to 4.43), standardized effect d = 0.05; z-test p = 0.632.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tio R5 qd and the control. The interval gives the range of effects that remain compatible with the data.

Across the posted secondary continuous outcomes, the group estimates are positive, and the confidence intervals include zero. This broad pattern is directionally consistent with the positive primary point estimate, but it does not add strong precision to the primary finding. The secondary outcomes concern related but distinct pulmonary-function measures, including FVC and FEF25-75, so they provide context rather than a substitute for the prespecified primary comparison.

The registry also lists pulmonary exacerbations and change in the revised Cystic Fibrosis Questionnaire score among the secondary outcomes, but corresponding results for those measures are not included in the posted secondary analyses described in the record. Their numerical findings are therefore not reported in the registry record. The record lists five secondary outcomes and posts results for three continuous measures.

Unadjusted secondary results carry less weight when several outcomes and analyses are examined. In general, repeated testing increases the chance that at least one result will appear notable by chance, even when no multiplicity adjustment is applied. The registry record does not report a multiplicity procedure or identify which secondary analyses, if any, were intended to be confirmatory. Their p-values should consequently be read as descriptive evidence rather than as a definitive collection of separate tests.

The secondary pattern should not be used to claim that all outcomes agree or that the treatment effect is established across measures. The posted results are limited to the outcomes reported, and uncertainty remains in each reported comparison. A broader conclusion would require complete outcome reporting and an analysis plan clarifying the role of these secondary endpoints.

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

• Forced Vital Capacity (FVC) Area Under the Curve 0-4 Hours (AUC0-4h) Response
• Trough FVC Response
• Pre-bronchodilator Forced Expiratory Flow Between 25 Percent and 75 Percent of the FVC (FEF25-75) Response
• Percentage of Participants With at Least 1 Pulmonary Exacerbation During Double-blind Treatment
• Change From Baseline in Revised Cystic Fibrosis Questionnaire (CFQ-R) Score

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary analysis estimate? The registry reports a mean difference between tiotropium and placebo in change from baseline in FEV1 AUC0-4h response. The endpoint is continuous, so the comparison is expressed in the endpoint’s units: percent of predicted. The reported group means are adjusted rather than simple averages of all recorded values. The mixed model includes treatment, visit, treatment-by-visit interaction, age group, baseline, and baseline-by-visit interaction. The age groups are specified as 11 years or younger and 12 years or older.

The registry describes the primary analysis as a Mixed Model Repeated Measurement (MMRM) analysis. In general, repeated-measures models use observations collected at multiple visits and model how outcome values relate across those visits. This can make use of the repeated structure rather than treating each time point as an unrelated comparison. The model’s treatment-by-visit term allows the treatment contrast to vary by visit. The registry gives the model terms but does not report a full statistical analysis plan, so details beyond those stated are not available in the registry record.

What do the mean and standard error convey? A mean summarizes the central value of a continuous measure. The standard error describes the precision of an estimated mean, not the spread of individual participant values. In general, a smaller standard error indicates a more precisely estimated mean under the analysis assumptions. It should not be interpreted as the range within which most individual responses fall. Comparing group means is useful, but the difference and its confidence interval give a more direct view of the estimated contrast and its uncertainty.

How is the area-under-the-curve measure constructed? The primary endpoint combines post-dose FEV1 measurements over the 0-to-4-hour interval. The registry says the AUC was normalized for time and calculated with the trapezoidal rule divided by the observation time of 4 hours. In general, the trapezoidal rule approximates the area under a curve by connecting observed values across time points and summing the resulting areas. Normalizing by observation time expresses the result as an average over the interval, rather than as an unscaled area that depends on the length of the observation period.

What is a confidence interval? A confidence interval gives a range of values compatible with the data and the statistical model at a stated confidence level. In general, a wider interval indicates less precision than a narrower interval. The primary reported 95% interval extends from -0.27 to 3.55. Since zero lies within that interval, the estimate does not rule out no difference at that confidence level. The interval also includes positive values, so the data remain compatible with a positive difference. It is not a guarantee that the true value lies within the interval, nor does it assign probabilities to individual values within it.

What does the p-value add? A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the model assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The registry’s primary p-value is 0.092. It should be considered alongside the estimate and confidence interval, not used as a standalone verdict. The registry record does not report enough detail to reconstruct every aspect of the modeling and testing procedure.

Why can over-dispersion matter? General statistical explanation: over-dispersion occurs when variability in the data is greater than a model assumes. If a model understates variability, standard errors can be too small and confidence intervals too narrow. The posted primary endpoint is continuous, and the registry identifies a mixed model with standard errors; it does not report an over-dispersion assessment. This concept is therefore general context, not a claim that over-dispersion occurred in this trial.

The simple re-calculation uses the posted arm means, standard errors, and sample sizes to make an unadjusted comparison. It is a descriptive check based on summary information, not a replacement for the registry’s mixed-model analysis. The adjusted and unadjusted results are close, but adjustment, repeated observations, and the analysis population can affect estimates and uncertainty. The record lists the sponsor’s model-based result as the trial analysis.

11. Confidence Intervals and Precision

The primary reported mean difference is 1.64 percent of predicted, with a 95% confidence interval from -0.27 to 3.55. This interval is the clearest guide to the precision of the estimated contrast. Its inclusion of zero means the posted analysis does not exclude no between-group difference. Its positive upper end and negative lower end also show that the estimate remains compatible with effects in either direction under the model and confidence procedure.

The simple unadjusted re-calculation produces a mean difference of 1.64, with a 95% confidence interval from -0.285 to 3.565. The interval is also broad enough to include zero. Its similarity to the reported model-based interval offers a check that the main numerical pattern is not driven by a large discrepancy between the simple summary-statistic calculation and the registry result. It does not make the analyses identical or remove the limitations of an unadjusted calculation.

Precision is not the same as whether an estimate is important. A narrow interval would indicate more precision, while a broad interval leaves more uncertainty about the size and direction of the difference. The standard errors reported for the group means are 0.8 for placebo and 0.57 for tiotropium. These describe the precision of the respective means, not the spread of individual participant outcomes. The confidence interval for the between-group contrast is more relevant to uncertainty about the primary comparison.

Neither the point estimate nor the interval alone establishes clinical importance. The registry record does not report a threshold for a clinically meaningful difference in this endpoint. The interval therefore supports a statistical description of uncertainty, but not a conclusion about whether the range would matter to patients or clinicians.

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, not the trial’s original design assumptions. The registry record does not report the original sample-size justification. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses the stated fraction of the observed effect as the effect to detect. For these continuous outcomes, the figures are participants per arm, not total participants or total events.

The 80% power column describes the number of participants per arm used in the planning illustration to give an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true effect and the model assumptions held. The 90% power column uses a higher target chance of detection, so it calls for more participants per arm for the same assumed effect. For example, planning for 100% of the observed primary effect gives 551 participants per arm for 80% power and 738 participants per arm for 90% power. Planning for 75% of the observed effect gives 980 participants per arm for 80% power and 1,312 participants per arm for 90% power.

The fractions represent planning scenarios, not observed treatment effects in new groups. Smaller effects are harder to distinguish from random variation, so detecting a smaller fraction of the observed effect requires more participants per arm. For the primary endpoint, planning for 50% of the observed effect gives 2,204 participants per arm for 80% power and 2,951 participants per arm for 90% power. Those figures are illustrations conditional on the stated assumptions, rather than recommendations or evidence about the trial’s original planning process.

This is not observed power. It does not describe the probability that the completed trial detected an effect after its results were known. The trial’s actual design assumptions, including the effect size used in its original planning, are 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 = 1.640; pooled standard deviation σ = 9.716.
2. n = 2 × (1.96 + 0.842)² × 9.716² / 1.640² = 550.9, rounded up to 551 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 <- 1.64                      # observed difference in means
sigma <- 9.71570689916378                     # 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(1179347)
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 = 551 (80% power), 738 (90% power)
 75% of observed effect: n per arm = 980 (80% power), 1,312 (90% power)
 50% of observed effect: n per arm = 2,204 (80% power), 2,951 (90% power)
power.t.test: 551.9 
Simulated power at n = 551 per arm: 0.797 (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 mixed-model analysis as a mean difference of 1.64, with a 95% confidence interval from -0.27 to 3.55 and p = 0.092. The simple unadjusted re-calculation from posted summary statistics gives a mean difference of 1.64, a 95% confidence interval from -0.285 to 3.565, and p = 0.095. The estimates are close, and both intervals include zero.

The re-calculation is not a reproduction of the mixed model. It uses the posted group-level means, standard errors, and sample sizes to form a simple comparison, without the model’s stated adjustment for treatment, visit, treatment-by-visit interaction, age group, baseline, and baseline-by-visit interaction. A small difference in interval endpoints or p-values is therefore not unexpected when the procedures differ.

The registry record does not mark a discrepancy between the posted analysis and the re-calculation. The sponsor’s reported model-based result remains the primary trial analysis because it is the analysis reported for the endpoint. The re-calculation serves as a transparent, unadjusted check and should not replace the trial’s stated analysis or be interpreted as an independent confirmation.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies a primary endpoint and several secondary outcomes, but it does not report whether the trial used a multiplicity adjustment. Multiplicity matters because testing several outcomes or contrasts can increase the chance of obtaining at least one apparently unusual result by chance. In general, an analysis plan can specify which outcome is primary, how secondary outcomes are ordered, and whether adjustments are used. The record does not provide enough information to establish such a strategy for this trial.

The record also does not report a complete description of missing-data methods for every outcome. For the primary endpoint, the population is described as the Full Analysis Set with imputation reduced to patients with observed wash-out compliance. The Full Analysis Set includes treated patients with at least one baseline pulmonary function test measurement and at least one post-baseline on-treatment pulmonary function test measurement. These definitions clarify who contributed to the analysis, but they do not fully explain how all missing measurements were handled or what assumptions supported any imputation.

The analysis population is not simply described as everyone randomized. The primary endpoint analysis is restricted by treatment, availability of baseline and post-baseline measurements, and observed wash-out compliance. The registry record does not give a complete participant-flow account that would permit a full assessment of how those restrictions affected the analyzed groups. Nor does it report sensitivity analyses for alternative missing-data assumptions.

The mixed model includes baseline and visit terms, but the presence of a model does not by itself resolve all possible bias from missing observations. General statistical explanation: missing-data methods rely on assumptions about why observations are absent; if those assumptions are not plausible, estimates can be sensitive to the missingness process. The registry record does not report enough information to evaluate those assumptions.

The registry record also does not report whether interim analyses were conducted, the detailed statistical analysis plan, or the original sample-size justification. These omissions limit assessment of the full testing strategy and the robustness of the reported inference. They do not change the posted numerical results, but they constrain how confidently the analysis process can be reconstructed from the 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: cystic fibrosis (4.8%), infective pulmonary exacerbation of cystic fibrosis (3.2%), lung disorder (2.9%), cystic fibrosis lung (2.0%), bronchitis (2.0%).

The serious adverse-event record gives at-risk counts and numbers affected for several treatment-period groupings. During the double-blind period, the placebo randomized group lists 13 affected among 155 at risk, and the tiotropium 5 mcg randomized group lists 36 affected among 308 at risk. These are counts of participants affected by at least one serious adverse event as represented in the registry; they are not a comparison adjusted for follow-up time or baseline risk.

Separate entries cover the open-label period for placebo and the study period for tiotropium. The placebo open-label entry lists 24 affected among 147 at risk; the tiotropium study entry lists 62 affected among 308 at risk. These entries cover different periods and should not be combined with the double-blind-period entries as though they were equivalent follow-up windows. The registry record does not report death counts.

The record lists serious-event terms including cystic fibrosis at 4.8%, infective pulmonary exacerbation of cystic fibrosis at 3.2%, lung disorder at 2.9%, cystic fibrosis lung at 2.0%, bronchitis at 2.0%, and pneumonia at 1.9%. These are descriptive registry listings. The figures alone do not establish that an event was caused by treatment, and they should not be treated as a complete comparative safety analysis.

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

The primary result describes a difference in mean change in FEV1 AUC0-4h response between the randomized groups over the 12-week double-blind treatment period. The posted model-based point estimate is 1.64 percent of predicted in favor of a higher mean change in the tiotropium group. Its 95% confidence interval, from -0.27 to 3.55, includes zero. The result therefore does not establish a clear between-group difference, and it does not prove that the groups were equivalent.

A failure to exclude zero is not evidence that the true difference must be zero. Rather, the posted data leave uncertainty about the direction and magnitude of the difference. The point estimate is one value within a wider range of results compatible with the analysis. The registry record does not report a threshold for clinical importance, so statistical results alone cannot say whether any possible difference within the interval would be meaningful to patients.

The trial’s findings apply to the endpoint, analysis population, treatment period, and methods described in the registry. The primary analysis used a defined Full Analysis Set and included a wash-out compliance restriction. The result should not be generalized beyond those conditions without additional evidence. In particular, the registry states that no patients under 5 years were included, and the findings do not provide direct information for that age group.

The secondary outcomes provide some related context, but their confidence intervals also include zero and the record does not report a multiplicity strategy. They should not be used to turn an uncertain primary estimate into a stronger claim. The safety listings are also descriptive and do not, by themselves, establish treatment causation or comparative risk.

In short, the registry reports a positive primary point estimate with substantial uncertainty around it. The available record supports describing that estimate and its precision, but not a categorical claim that tiotropium does or does not produce a particular clinical benefit.

18. Why This Trial Matters Statistically

This trial is statistically informative because it tests a pulmonary-function endpoint in a cystic fibrosis population using a randomized, double-blind, placebo-controlled design. Randomization and masking are design features intended, in general, to reduce systematic differences and influence on outcome assessment. The parallel-group comparison also makes the treatment contrast explicit. These design features strengthen interpretation of the reported comparison, while the endpoint definition and analysis population remain important to understanding what was estimated.

The primary measure captures FEV1 response across a post-dose interval rather than at a single time point. Combining repeated measurements into a time-normalized AUC can summarize a response pattern, but it also makes the calculation and model choices relevant to interpretation. The registry gives the measurement schedule, normalization procedure, and core model terms, allowing readers to understand the broad analytical approach.

Equally important is the uncertainty. A positive point estimate may attract attention, but the confidence interval includes zero and spans both negative and positive values. This makes precision central to the interpretation. Reporting the model-based estimate beside a transparent simple re-calculation helps readers see that the broad conclusion is not dependent on a large numerical disagreement between the two approaches, while preserving the distinction between an adjusted model and an unadjusted summary-statistic calculation.

The record also illustrates why a registry result must be read with attention to analysis populations, secondary outcomes, and safety time periods. Different counts apply to the primary endpoint and adverse-event summaries, and the adverse-event entries cover different treatment periods. Missing details about multiplicity, missing-data handling, and original design assumptions limit reconstruction of the analysis plan. These are not merely technical footnotes: they determine how far a reader can extend the inference beyond the reported estimate.

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 primary endpoint result is available as a model-based estimate, but the registry record does not provide a complete statistical analysis plan. It gives the central mixed-model terms without fully documenting all modeling choices, diagnostic checks, or sensitivity analyses. This limits independent reconstruction of the reported inference.

The primary analysis population is defined by treatment, baseline and post-baseline pulmonary-function measurements, and observed wash-out compliance. The record does not provide a complete participant-flow description or a full account of missing measurements. It also does not report the assumptions behind imputation or sensitivity analyses for missing-data mechanisms. The effect of these population restrictions and missing-data choices therefore cannot be fully assessed from the registry record.

The record lists several secondary outcomes but posts results for only some of them. It does not report whether multiplicity was addressed or which secondary outcomes were intended to support confirmatory conclusions. Results not posted in the record cannot be inferred from the outcomes’ inclusion in the registry.

The safety entries use different groupings and observation periods, including the double-blind period, open-label period, and study period. Those summaries are not directly interchangeable, and death counts are not reported in the registry record. The listed event terms and percentages also do not establish causality.

Finally, the registry record does not report the original sample-size justification, allocation ratio, or whether interim analyses occurred. Its planning illustrations based on the observed effect cannot fill those gaps or establish the assumptions used when the trial was designed. No patients under 5 years were included, which limits direct applicability of these results to that age group.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Tiotropium Bromide in Cystic Fibrosis — NCT01179347.
• Registry record last updated 2013-12-24; status last verified 2013-10.
• Results first posted 2013-03-26.
• 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

NCT01179347 is a completed phase 3 randomized, double-blind, placebo-controlled, parallel-group trial of tiotropium Respimat® in cystic fibrosis. The registry lists enrollment as 464. The primary endpoint was change from baseline in FEV1 AUC0-4h response after 12 weeks, expressed as percent of predicted.

The sponsor’s mixed-model analysis reports a mean difference of 1.64, with a 95% confidence interval from -0.27 to 3.55 and p = 0.092. The interval includes zero, leaving uncertainty about the direction and size of the difference. The registry also lists secondary pulmonary-function outcomes and adverse-event summaries, with limitations in outcome coverage and detail about analysis procedures.

The record describes the primary analysis population and model terms, but does not report the original sample-size justification, multiplicity procedure, full missing-data approach, or complete statistical analysis plan. The results should be interpreted as estimates for the population, endpoint, and treatment period specified in the registry.