Co-administration of Olodaterol Respimat® and Tiotropium Handihaler®: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Co-administration of Olodaterol Respimat® and Tiotropium Handihaler® (NCT01694771), a randomized phase 3 study. The primary outcome is FEV1 AUC0-3h Response at 12 Weeks; Defined as Change From Baseline to Week 12.

2. Clinical Question

The clinical question is about the average difference in lung-function response between these assigned regimens in the trial population. It does not directly ask whether either regimen is better than no treatment, nor does the primary endpoint describe symptoms, exacerbations, or long-term outcomes. Those distinctions matter when interpreting the result: the registry record reports a comparison of two co-administered regimens over 12 weeks, focused on a spirometric measure.

3. Trial Design

The registry record describes a completed Phase 3 randomized, double-blind, parallel-group study. The trial compared once-daily co-administration of olodaterol and tiotropium with once-daily co-administration of matching placebo and tiotropium in patients with COPD. The intervention and comparator shared tiotropium, so the randomized contrast concerns adding olodaterol rather than initiating tiotropium.

The planned enrollment was 1134. For the primary outcome, the posted arm summaries report 563 participants in the olodaterol-plus-tiotropium group and 564 in the placebo-plus-tiotropium group. These are endpoint analysis counts; the registry record separately reports enrollment. The primary analysis population was the full analysis set with last observation carried forward (LOCF) imputation at 12 weeks. The definition refers to treated patients who had a baseline and at least one post-baseline measure at or before 12 weeks for any co-primary efficacy variable.

Masking is recorded as double, allocation as randomized, and the model as parallel. These design features support an interpretation based on a randomized comparison, while the registry record does not describe the details of sequence generation or how masking was maintained. The study’s stated duration for the efficacy assessment was 12 weeks. Start and primary-completion dates are recorded, but they are not needed to interpret the treatment contrast.

The registry record does not report the original sample-size justification, the planned statistical analysis in full, or details of any interim analyses. It also does not give enough information to reconstruct participant flow or to assess the success of masking. Those omissions limit appraisal of some design choices, even though the basic randomized comparison and its primary outcome are identifiable.

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: 1134 patients were entered and randomized to treatment and 1132 patients were treated with study medication.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS) with last observation carried forward (LOCF) imputation at 12 weeks. FAS included all patients in the treated set who had both baseline and at least one post-baseline measurement at or before 12 weeks for any of the co-primary efficacy variables

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), which includes all randomized patients who receive at least one dose of double-blind study treatment.

6. Primary Endpoint

The registry lists the primary outcome as FEV1 AUC0-3h Response at 12 Weeks; Defined as Change From Baseline to Week 12, measured over baseline and 12 weeks.

The primary endpoint is the change from baseline to Week 12 in FEV1 AUC0-3h, reported in liters as an area-under-the-curve measure. FEV1 is forced expiratory volume in 1 second; AUC0-3h summarizes measurements across the first 3 hours rather than representing a single measurement at one time point. A change-from-baseline endpoint compares the follow-up response with each participant’s starting measurement.

AUC measures can summarize a response over a period and may capture more information about the time course than a single measurement. In this trial, the endpoint was used to assess lung-function response after once-daily co-administration of the assigned inhaled regimens. It is a continuous outcome, so the posted arm results are least-squares means and the treatment contrast is expressed as a mean difference.

The primary outcome’s analysis population was the full analysis set with LOCF imputation at 12 weeks. The registry definition requires treated patients to have baseline and at least one post-baseline measurement at or before 12 weeks for any co-primary efficacy variable. LOCF carries a participant’s last recorded observation forward to the designated endpoint when later data are unavailable. That approach depends on assumptions about what the unobserved outcome would have been; the registry record does not report sensitivity analyses addressing those assumptions.

The endpoint describes a particular lung-function measure over a limited follow-up period. It should not be interpreted as a direct measure of every aspect of COPD or as evidence about outcomes beyond the period recorded.

7. Results Posted in the Registry

• Olodaterol (5µg) and Tiotropium (18µg): mean 0.31 versus 0.20 on control; difference 0.12 (95% CI 0.09 to 0.14), standardized effect d = 0.49; 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.

Peak FEV1 Response at 12 Weeks - Defined as 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:
  • Olodaterol (5µg) and Tiotropium (18µg): mean 0.39 versus 0.27 on control; difference 0.12 (95% CI 0.09 to 0.15), standardized effect d = 0.50; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Olodaterol (5µg) and Tiotropium (18µg) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

FVC AUC0-3h Response at 12 Weeks - Defined as 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:
  • Olodaterol (5µg) and Tiotropium (18µg): mean 0.44 versus 0.29 on control; difference 0.15 (95% CI 0.10 to 0.19), standardized effect d = 0.36; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Olodaterol (5µg) and Tiotropium (18µg) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Trough FVC Response at 12 Weeks- Defined as 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:
  • Olodaterol (5µg) and Tiotropium (18µg): mean 0.28 versus 0.21 on control; difference 0.06 (95% CI 0.02 to 0.11), standardized effect d = 0.17; z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Olodaterol (5µg) and Tiotropium (18µg) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary lung-function question to peak FEV1 response, FVC responses, and several measures of rescue-medication use. The posted lung-function contrasts generally favor the olodaterol-plus-tiotropium group, including the primary outcome’s broader pattern across peak and FVC measures. The registry also lists rescue-free days and total, daytime, and nighttime rescue use as secondary outcomes. Their presence indicates that the study assessed more than a single spirometric summary, but the record does not establish that every secondary outcome supports the same conclusion.

The secondary measures are related to the primary result because they assess other aspects of lung function or medication use during the same treatment comparison. They are not interchangeable with the primary FEV1 AUC0-3h outcome. A consistent direction across related measures can add context, but does not create independent proof: measures from the same participants and study may be correlated, and the registry record does not report how that dependence was handled across outcome testing.

Unadjusted secondary p-values carry less weight when many outcomes are examined. In general, repeated testing increases the chance that at least one result appears noteworthy by chance. A multiplicity adjustment or a prespecified testing hierarchy can help control that risk, but the registry record does not report whether one was used for the secondary outcomes. The posted secondary results should therefore be treated as supportive or exploratory evidence rather than as a collection of equally confirmatory findings.

The record identifies ten outcome measures and ten analyses overall, while only some secondary results are posted in the trial record. It reports eight secondary outcomes by name, and the available secondary statistical summaries cover the lung-function endpoints listed in the record. The registry record does not provide complete results for every named secondary outcome, so the overall direction of rescue-medication findings cannot be determined from these data alone. No secondary result should be inferred where a result is not reported.

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

• Peak FEV1 Response at 12 Weeks - Defined as Change From Baseline
• FVC AUC0-3h Response at 12 Weeks - Defined as Change From Baseline
• Trough FVC Response at 12 Weeks- Defined as Change From Baseline
• Peak FVC Response at 12 Weeks - Defined as Change From Baseline
• Rescue Medication Usage - Percentage of Rescue Free Days
• Rescue Medication Usage - Mean Weekly Rescue Usage (Total Daily)
• Rescue Medication Usage - Mean Weekly Rescue Usage (Daytime)
• Rescue Medication Usage - Mean Weekly Rescue Usage (Nighttime)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary measure is continuous, and the registry reports least-squares means for the two groups. A least-squares mean is a model-based estimate of the group mean, potentially accounting for terms included in the fitted model. The registry identifies a mixed model repeated-measure method for the sponsor’s primary contrast, but does not report all model terms, covariance assumptions, or details needed to reproduce the fit. Interpretation of the reported estimate therefore relies on the sponsor’s stated model result rather than an independent reconstruction of that model.

What does the mean difference represent?

The mean difference is the estimated contrast between the olodaterol-plus-tiotropium group and the placebo-plus-tiotropium group for change in FEV1 AUC0-3h. A positive estimate indicates a higher average change in the group receiving olodaterol plus tiotropium, given the direction of subtraction in the reported comparison. The result is an average contrast; it does not describe how responses varied among individual participants.

The group estimates are 0.313 and 0.196, and the reported model-based difference is 0.117. The unit is liters for the AUC measure. The registry’s primary result is described as a mean difference in final values by the analysis record, while the endpoint itself is defined as change from baseline. This naming difference should not be used to infer a different outcome: the registry’s endpoint description and the sponsor’s reported analysis should be read together.

What does the repeated-measures model do?

A repeated-measures model is generally used when outcome observations are collected at multiple time points for the same participants. It can account for the fact that measurements from the same participant are related, rather than treating every observation as independent. The registry record identifies a mixed model repeated-measure analysis, but does not report its full specification, including the covariance structure, fixed effects, or handling of all incomplete measurement patterns. The exact assumptions and implementation therefore cannot be evaluated from the record alone.

The posted recalculation is different. It is an unadjusted calculation from the arm summaries, using an approximate pooled standard deviation. The posted standard errors are 0.01 for both primary arm means. Because the standard deviation is approximated from summary information, this calculation is illustrative rather than a reproduction of the sponsor’s model. It produces a mean difference of 0.117 and a 95% confidence interval from 0.089 to 0.145, with p <0.001. The sponsor reports a model-based 95% confidence interval from 0.090 to 0.144 and p < 0.001.

Why can estimates from the analyses differ?

Analyses can differ because they use different information and assumptions. A repeated-measures model uses the longitudinal outcome structure specified by the analyst, whereas the simple recalculation operates on posted group summaries. Model adjustment, the handling of within-participant correlation, and rounding can affect the estimated uncertainty. Here the reported effect estimates are the same at the displayed three-decimal precision, while the confidence limits and p-values differ slightly. The registry record does not provide enough model detail to identify the contribution of each factor.

What is a p-value?

In general, a p-value measures how incompatible the observed data, or data more extreme, are with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true, nor a measure of the size or practical importance of an effect. The sponsor reports p < 0.001 for the primary comparison, while the unadjusted recalculation reports p <0.001. Both are reported as evidence against a zero mean difference under their respective methods; neither quantifies clinical importance.

Why does over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a statistical model’s assumed variability. It is most directly relevant to outcomes modeled as counts or other discrete data, rather than to a continuous mean difference such as the primary endpoint. If a model fails to account for extra variability, its standard errors and confidence intervals can be too small, making results appear more precise than warranted. The registry record does not report an over-dispersion assessment for the primary continuous outcome, so no trial-specific conclusion about it can be made.

The primary analysis uses LOCF imputation at 12 weeks in the defined full analysis set. As a general method, LOCF replaces a missing later measurement with the last available measurement. This can simplify an analysis but may not represent the unobserved outcome if participants’ status changes after their last measurement. The registry record does not report sensitivity analyses or alternative missing-data methods, so the robustness of the primary result to missing-data assumptions cannot be judged from this record.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is a mean difference of 0.117, with a 95% confidence interval from 0.090 to 0.144. The interval describes a range of values reasonably compatible with the observed data and the model assumptions, using the stated confidence procedure. It is not a range containing 95% of individual participant outcomes, and it does not guarantee that the true effect lies in the interval.

The interval is entirely above zero, consistent with the reported p < 0.001 for testing a zero difference. Its endpoints also show that the estimate is not infinitely precise: a range of mean differences remains compatible with the data and analysis. The confidence interval expresses statistical uncertainty, not clinical importance. The registry record does not specify a threshold for a clinically important change, so the interval cannot be compared with such a threshold from this information.

The unadjusted recalculation gives a 95% confidence interval from 0.089 to 0.145. Its close agreement with the sponsor interval supports the view that the primary contrast is not an artifact of the simplified calculation, but the recalculation depends on an approximate standard deviation and does not replace the sponsor’s repeated-measures analysis. The registry record does not provide full model specifications that would allow independent verification of the reported model-based precision.

Confidence intervals address uncertainty in an estimated average contrast under the analysis method. They do not describe the spread of responses among participants, and they do not include every source of uncertainty, such as uncertainty from outcome selection, missing-data assumptions, or departures from the model. The primary population and LOCF approach are specified, but sensitivity analyses are not reported in the registry record.

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 are participants per arm for 80% power and participants per arm for 90% power. They 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. The effect used for each planning scenario is the stated fraction of the observed effect. For example, planning for 75% of the observed effect means using a smaller target difference than the full observed estimate. Smaller effects need more participants to achieve the same target power.

The 80% power column gives an approximate per-arm sample size for a design with an 80% chance of detecting the assumed effect at the stated significance level, if that effect and the calculation assumptions were correct. The 90% power column expresses the same planning idea with a higher target chance of detection, which generally requires more participants per arm. These are conditional design calculations, not guarantees that a future study will obtain a particular result.

For these continuous outcomes, the entries are participants per arm, not total events. The record’s general planning note distinguishes these figures from time-to-event calculations, which use total events, but the outcomes are continuous. These values are not observed power: they are prospective planning illustrations based on the observed effect and stated assumptions. They should not be read as the sample-size rationale used to plan the completed trial.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.117; pooled standard deviation σ = 0.237.
2. n = 2 × (1.96 + 0.842)² × 0.237² / 0.117² = 64.6, rounded up to 65 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 <- 0.117                      # observed difference in means
sigma <- 0.237381643023306                     # 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(1694771)
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 = 65 (80% power), 87 (90% power)
 75% of observed effect: n per arm = 115 (80% power), 154 (90% power)
 50% of observed effect: n per arm = 259 (80% power), 347 (90% power)
power.t.test: 65.6 
Simulated power at n = 65 per arm: 0.793 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor reports a mixed model repeated-measure analysis for the primary comparison. It gives a mean difference of 0.117, a 95% confidence interval from 0.090 to 0.144, and p < 0.001. This is the trial’s reported analysis and should be distinguished from the simple unadjusted recalculation based on the posted arm summaries.

The recalculation also gives an estimated mean difference of 0.117, with a 95% confidence interval from 0.089 to 0.145 and p <0.001. The agreement in the displayed point estimate is close; the interval limits and p-values differ because the methods are not identical. The recalculation uses an approximate pooled standard deviation derived from summary statistics, while the sponsor’s analysis is a repeated-measures model.

The registry record does not indicate a discrepancy between the posted sponsor result and the recalculation. The recalculation is therefore best understood as a consistency check, not a substitute for the sponsor’s analysis or an independent reconstruction of its model. The record does not report enough details about the model to reproduce it fully. Interpretation should retain the sponsor’s stated analysis method and the limits of what can be independently checked from the posted summaries.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study assesses several outcomes, time points, or treatment contrasts. Even if each individual test uses a conventional significance threshold, repeated testing can increase the chance of at least one apparently positive result under a setting where no effects exist. General approaches include adjusting significance thresholds, controlling a family-wise error rate, or defining an ordered testing strategy. The registry record does not report whether the primary and secondary outcomes were subject to such a strategy.

The primary endpoint is clearly identified, and its sponsor-reported analysis has a confidence interval above zero with p < 0.001. That result can be described as the reported primary comparison. However, the record does not report the full prespecified statistical plan, the relationship among any co-primary outcomes, or whether testing of secondary endpoints was gated on primary results. The phrase in the analysis-population definition refers to co-primary efficacy variables, but the registry entries available do not fully explain the co-primary testing framework.

Missing-data handling is relevant because the primary population uses LOCF imputation at 12 weeks. The stated full analysis set includes treated patients with a baseline and at least one post-baseline measurement at or before 12 weeks for any co-primary efficacy variable. LOCF carries the last observed value forward when a later value is unavailable. In general, this assumes that the carried-forward value is an adequate substitute for the unobserved endpoint, an assumption that may not hold if outcomes change over time.

The registry record does not report the amount or pattern of missing primary outcome data, reasons for missingness, or sensitivity analyses using alternative assumptions. It also does not report whether imputation was performed before or within the repeated-measures analysis beyond the stated LOCF description. Without those details, the impact of missing data on the estimate cannot be assessed fully.

The record identifies the full analysis set, but does not provide a complete flow of randomized, treated, and analyzed participants for every endpoint. The primary arm counts and the safety counts differ because they refer to different analysis contexts; the registry record does not explain all reasons for those differences. These omissions constrain assessment of population-specific selection and robustness.

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: chronic obstructive pulmonary disease (2.5%), pneumonia (0.5%), acute respiratory failure (0.5%), cardiac failure congestive (0.4%), myocardial infarction (0.4%).

The registry reports serious adverse events for 40 of 567 participants at risk in the olodaterol-plus-tiotropium group and 26 of 565 participants at risk in the placebo-plus-tiotropium group. It separately reports other adverse events affecting 60 of 567 and 52 of 565 participants at risk, respectively. These are counts of participants affected in the registry’s safety summaries, not estimates of comparative risk adjusted for follow-up or other factors.

The record lists serious-event terms and percentages, including chronic obstructive pulmonary disease at 2.5%, pneumonia at 0.5%, acute respiratory failure at 0.5%, cardiac failure congestive at 0.4%, myocardial infarction at 0.4%, and chest pain at 0.4%. The registry record does not specify a group attribution for these listed terms in the information, so they should not be assigned to an arm. Death counts are not reported in the registry record.

These summaries describe events recorded during the trial; they do not by themselves establish that treatment caused an event or that one regimen is safer. The registry record does not provide enough detail about event definitions, exposure time, severity beyond the serious-event designation, or adjudication to support a fuller comparative safety assessment.

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

The primary finding is a positive average difference in change in FEV1 AUC0-3h for olodaterol plus tiotropium compared with placebo plus tiotropium at 12 weeks. The sponsor’s model-based estimate is 0.117, with a 95% confidence interval from 0.090 to 0.144 and p < 0.001. The interval excludes zero under the reported analysis, indicating statistical evidence of a difference between the randomized regimens.

This result does not establish how much an individual participant would change, whether the average difference is clinically important, or how it compares with a threshold meaningful to patients. The registry record does not report a clinically important difference for this endpoint. A statistically precise estimate and a clinically important effect are related but separate questions.

The finding also does not compare the combination with no treatment: both groups received tiotropium. It addresses the addition of olodaterol to tiotropium, relative to adding matching placebo, in the trial’s COPD population. The result is specific to the endpoint definition, the analysis population, the imputation approach, and the 12-week period described in the record.

It does not establish effects on longer-term outcomes, exacerbations, symptoms, quality of life, or outcomes not reported in the registry record. Nor does it establish safety beyond the trial’s recorded follow-up. The secondary outcomes may provide context, but multiplicity and incomplete reporting mean they should not be treated as equivalent to the primary endpoint.

The appropriate reading is therefore bounded: the posted results support a difference in the specified mean lung-function endpoint under the sponsor’s analysis, while leaving clinical importance, long-term consequences, and robustness to unreported assumptions unresolved.

18. Why This Trial Matters Statistically

This trial illustrates how a randomized comparison can isolate the contrast between adding an inhaled medicine and adding a matching placebo when background treatment is held in common. The comparator is not an untreated group; it is tiotropium plus placebo. Making that contrast explicit prevents a common interpretive error about what the randomized estimate represents.

It also shows why the outcome definition matters. FEV1 AUC0-3h summarizes a lung-function response over a specified interval, while peak FEV1, trough FVC, and other outcomes represent related but different measurements. A statistically clear contrast for one measure does not automatically answer questions about symptoms, long-term disease course, or other outcomes.

The comparison between the sponsor’s repeated-measures analysis and an unadjusted recalculation illustrates how a point estimate can be stable while confidence limits and p-values vary with methods and assumptions. Reporting the sponsor’s method alongside a transparent summary-based check helps readers understand what can be reproduced and what depends on model details not fully reported in the registry.

Finally, the record demonstrates the importance of separating efficacy estimates from planning calculations and safety summaries. Planning figures use assumptions to illustrate future sample sizes; they are not observed power. Adverse-event counts describe what was recorded, but do not establish causation. Keeping these interpretations distinct supports careful statistical reading without turning a single short-term endpoint into a broader clinical claim.

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 gives the primary endpoint, population definition, sponsor’s effect estimate, and repeated-measures method, but does not provide the full statistical model specification. Covariance assumptions, model terms, and detailed handling of incomplete repeated measurements are not reported in the registry record. This limits independent reproduction of the sponsor’s analysis.

The primary population uses LOCF imputation, but the record does not report the amount or pattern of missing data, reasons for missingness, or sensitivity analyses. The resulting estimate may depend on assumptions about outcomes after the last recorded measurement. The registry record also does not report the original sample-size justification, so the planning illustrations cannot be taken as evidence of the design rationale.

The registry record does not report whether multiplicity was controlled across co-primary and secondary outcomes. It names several secondary measures, but complete outcome results are not available for every one in the record. As a result, secondary patterns cannot be fully assessed, and unadjusted findings should be interpreted cautiously.

The posted arm counts vary by analysis context: primary efficacy summaries, safety summaries, and other endpoints have different reported counts. The record does not give a full participant-flow account to explain all differences. Safety data are summarized as affected counts, without enough detail to assess exposure time, event attribution, or comparative causal risk. Death counts are not reported in the registry record.

Follow-up for the efficacy question is limited to 12 weeks. These registry results therefore do not answer questions about longer-term effects or outcomes not reported in the record. The stated design is randomized and double-blind, but procedural details about randomization and masking are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Co-administration of Olodaterol Respimat® and Tiotropium Handihaler® — NCT01694771.
• Registry record last updated 2014-09-04; status last verified 2014-08.
• Results first posted 2014-09-04.
• 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

The registry record describes a completed Phase 3 randomized, double-blind, parallel-group study in patients with COPD. It compared once-daily olodaterol 5µg plus tiotropium 18µg with matching placebo plus tiotropium 18µg over 12 weeks. Planned enrollment was 1134.

The primary outcome was change from baseline in FEV1 AUC0-3h. The sponsor reported a mean difference of 0.117, with a 95% confidence interval from 0.090 to 0.144 and p < 0.001 using a mixed model repeated-measure analysis. A simple unadjusted recalculation gives a similar point estimate, with somewhat different uncertainty limits.

Secondary outcomes include additional lung-function and rescue-medication measures. The record does not report a full multiplicity plan or all details needed to reproduce the primary model. Safety summaries report serious and other adverse-event counts; death counts are not reported in the registry record. Interpretation is limited to the recorded outcomes, analysis population, and follow-up.