Comparing the Efficacy of Tiotropium + Olodaterol (5/5 µg) Fixed Dose Combination (FDC) Over Tiotropium 5µg in Reducing Moderate to Severe Exacerbations in Patients With Severe to Very Severe Chronic Obstructive Pulmonary Disease.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparing the Efficacy of Tiotropium + Olodaterol (5/5 µg) Fixed Dose Combination (FDC) Over Tiotropium 5µg in Reducing Moderate to Severe Exacerbations in Patients With Severe to Very Severe Chronic Obstructive Pulmonary Disease. (NCT02296138), a randomized phase 3 study. The primary outcome is Annualised Rate of Moderate to Severe COPD Exacerbations During the Actual Treatment Period..

2. Clinical Question

The question concerns the frequency of qualifying exacerbations over participants’ treatment exposure. This distinction matters because participants may contribute different amounts of time to the actual treatment period. An annualised rate uses that exposure time in expressing the outcome, whereas a count of patients with at least one event treats the outcome as whether or not a person experienced an event. The registry also posted secondary outcomes about patients experiencing exacerbations and about hospitalisation, but these address related, not identical, questions.

3. Trial Design

DYNAGITO was a Phase 3 randomized, double-blind, parallel-group, active-controlled study sponsored by Boehringer Ingelheim. It compared once-daily tiotropium plus olodaterol fixed-dose combination with once-daily tiotropium in patients with severe to very severe COPD. Both treatments were delivered using the Respimat inhaler. The registry lists enrollment of 7903 and marks the study completed.

The study started on 2015-01-13, with primary completion on 2017-03-08. The primary outcome timeframe ran from the first intake of study medication until one day after the last intake, up to 361 days. The registry defines the primary analysis population as the treated set, comprising randomized patients documented to have taken at least one dose of trial medication. The arm-specific treated populations reported for the primary outcome were 3941 for tiotropium and 3939 for the combination.

Random allocation and double masking are recorded, as is a parallel-group model. These design features support a direct comparison between the treatment groups, but the registry record does not report the details of the randomization procedure, how masking was maintained, or how treatment adherence was handled. The planned sample-size justification and original design assumptions are not reported in the registry record. The sample-size calculations discussed separately are planning illustrations based on the observed effect, not the study’s original design plan.

The primary endpoint was an annualised rate of moderate to severe COPD exacerbations during actual treatment. Secondary outcomes included patients with at least one moderate to severe exacerbation, exacerbation rates leading to hospitalisation, patients with a hospitalisation-leading exacerbation, and all-cause mortality. The registry record lists five outcome measures overall and eight analyses, but does not report enough detail to establish the full prespecified analysis hierarchy.

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: Following informed consent, the patient was entered into a maximum 7-day screening period to confirm the patient's eligibility. At Visit 2, after a successful review of the inclusion and exclusion criteria, the patient was randomly allocated in equal ratio to receive once daily trial treatment and then entered the 360 days treatment phase.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Treated set (TS) -This patient set includes all randomised patients who were documented to have taken at least 1 dose of trial medication.

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 includes all randomised patients who were documented to have taken at least 1 dose of trial medication.

6. Primary Endpoint

The registry lists the primary outcome as Annualised Rate of Moderate to Severe COPD Exacerbations During the Actual Treatment Period., measured over From first in-take of study medication until 1 day after last in-take of study medication, up to 361 days.

The primary endpoint was the annualised rate of moderate to severe COPD exacerbations during the actual treatment period, expressed as a rate per patient-year. The period began with the first intake of study medication and ended one day after the last intake, with a maximum timeframe of 361 days. The registry says the reported least-squares means are exponentiated.

A rate endpoint describes the number of events relative to time at risk or exposure. It can therefore incorporate follow-up time when participants do not all contribute the same duration of treatment observation. That makes it different from a binary endpoint, such as whether a participant had at least one exacerbation. A participant can experience more than one event, and a rate can reflect repeated events as well as exposure duration.

Rate endpoints are useful when the clinical question concerns event frequency over time rather than only the occurrence of a first event. They also require an analysis that accounts appropriately for the distribution of event counts and the amount of exposure. The registry reports that the primary sponsor analysis used a negative binomial model. The analysis details beyond the stated endpoint, model, and reported estimates are not reported in the registry record.

The posted arm estimates were 0.97 exacerbations per patient-year for tiotropium and 0.9 for the combination. These are group-level estimated rates; they do not describe the experience of every participant. The comparison between groups, and its uncertainty, is needed to assess how precisely the observed difference is estimated.

7. Results Posted in the Registry

• Tiotropium (5 μg) + Olodaterol (5 μg): 0.90 versus 0.97 (Rate per patient-year) on control; rate ratio 0.93 (95% CI 0.39–2.22, approximate, Poisson model); p ≈ 0.867.

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.

Number of Patients With at Least One Moderate to Severe COPD Exacerbation During the Actual Treatment Period.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Tiotropium (5 μg) + Olodaterol (5 μg): 44.3% (1746/3939) versus 45.1% (1777/3941) on control; risk difference -0.8 percentage points (95% CI -3.0 to 1.4), risk ratio 0.98 (0.94–1.03); unadjusted two-proportion z-test p = 0.495.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tiotropium (5 μg) + Olodaterol (5 μg) and the control. The interval gives the range of effects that remain compatible with the data.

Annualised Rate of Exacerbations Leading to Hospitalisation During the Actual Treatment Period.

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, with the standard error taken from the posted confidence limits.
• Result:
  • Tiotropium (5 μg) + Olodaterol (5 μg): 0.18 versus 0.20 (Rate per patient-year) on control; rate ratio 0.90 (95% CI 0.77–1.05, derived from the posted confidence limits); p ≈ 0.169.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Tiotropium (5 μg) + Olodaterol (5 μg) and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients With at Least One COPD Exacerbation Leading to Hospitalisation During the Actual Treatment Period.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Tiotropium (5 μg) + Olodaterol (5 μg): 11.4% (450/3939) versus 11.9% (469/3941) on control; risk difference -0.5 percentage points (95% CI -1.9 to 0.9), risk ratio 0.96 (0.85–1.08); unadjusted two-proportion z-test p = 0.510.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tiotropium (5 μg) + Olodaterol (5 μg) and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary outcomes, the posted estimates generally point in the same numerical direction as the primary comparison, with estimates favoring the combination on event frequency or time to an event. However, the secondary comparisons are less conclusive: the sponsor-reported confidence intervals include the relevant no-difference value, and the reported p-values do not establish a clear separation between groups. The overall pattern is therefore compatible with the direction of the primary estimate, but it does not independently settle the uncertainty in the primary result.

These outcomes are related but not interchangeable. The count of participants with at least one exacerbation does not capture repeated events in the same way as an annualised rate. Hospitalisation-leading exacerbations are a narrower event category, and time-to-event analyses address when an event occurs as well as whether it occurs. The mortality outcome is another distinct endpoint. A consistent direction across endpoints can be informative, but different definitions and statistical methods mean that the estimates need not match.

Secondary findings carry less weight when their tests are unadjusted for multiplicity. Testing several outcomes increases the chance that at least one result may appear statistically notable by chance. The registry record does not report a multiplicity adjustment or a hierarchy that would establish which secondary tests were confirmatory. Consequently, isolated secondary p-values should be treated as exploratory unless the analysis plan says otherwise; that plan is not reported in the registry record.

The secondary results add context about event occurrence and hospitalisation, but they do not replace the primary rate analysis. They also do not remove the need to consider confidence intervals, analysis populations, and the status of the tests within the study’s planned statistical strategy.

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

• Number of Patients With at Least One Moderate to Severe COPD Exacerbation During the Actual Treatment Period.
• Annualised Rate of Exacerbations Leading to Hospitalisation During the Actual Treatment Period.
• Number of Patients With at Least One COPD Exacerbation Leading to Hospitalisation During the Actual Treatment Period.
• Number of Patients With All-cause Mortality Occurring During the Actual Treatment Period.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a count rate: qualifying exacerbation events are considered in relation to patient-year exposure. The registry reports least-squares means that are exponentiated and identifies a negative binomial model for the sponsor’s primary analysis. The model produces a ratio of rates comparing the combination with tiotropium. A ratio of 1 represents equal rates; a ratio below 1 indicates a lower estimated rate in the combination group, and a ratio above 1 indicates a higher estimated rate. This is a general interpretation of a rate ratio, not a claim about the clinical importance of any particular value.

Why use a negative binomial model?

General statistical explanation: count outcomes often show over-dispersion, meaning their variability is greater than would be expected under a simple Poisson model with a single mean rate. Repeated events can cluster in some participants, and event counts can vary substantially across participants. A negative binomial model allows for this extra variability. If over-dispersion is present but not accommodated, uncertainty estimates from a simpler model can be too small. The registry identifies a negative binomial model for the sponsor analysis but does not report a dispersion estimate or diagnostic assessment.

The simple recalculation uses posted arm-level rates and event information under a Poisson approach. It is labelled recalculated because it is an unadjusted reconstruction from summary statistics, not the trial’s fitted model. Its interval and p-value differ markedly from the sponsor’s analysis. Since the record flags a discrepancy, the sponsor’s own analysis takes precedence; the recalculation should not be treated as an alternative trial result of equal standing. The registry record does not provide sufficient model details to reproduce the sponsor analysis independently.

What does a confidence interval convey?

General statistical explanation: a confidence interval describes the range of estimates compatible with the data and the method at the stated confidence level. A narrower interval indicates greater precision under that method; a wider interval indicates greater uncertainty. For a ratio, an interval containing 1 includes the no-difference value. An interval that excludes 1 is often described as statistically distinguishable from no difference at the corresponding confidence level, subject to the analysis plan and multiplicity considerations. The primary sponsor interval runs from 0.85 to 1.02 at the 99% level, so it includes 1.

How should the p-value be read?

General statistical explanation: a p-value measures how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions held. It is not the probability that the null hypothesis is true, nor a measure of the size or clinical importance of an effect. The sponsor reports p = 0.050 for the primary comparison. The registry does not report the complete testing plan, including whether or how multiplicity was handled. That limits interpretation of the p-value as a standalone decision rule.

The posted secondary analyses use different forms of outcome and analysis. Some are rates analyzed with negative binomial models; others concern whether an individual experienced an event and use log-rank analyses with hazard ratios. A hazard ratio compares event rates over time under a time-to-event framework, while a rate ratio compares event counts per exposure. These quantities answer related but distinct questions and should not be treated as interchangeable. The registry record does not report the full assumptions, covariate adjustments, censoring rules, or missing-data procedures for every analysis.

11. Confidence Intervals and Precision

The primary sponsor estimate is a rate ratio of 0.93, with a 99% confidence interval from 0.85 to 1.02. The interval is the central guide to precision: it spans values below and above 1, so it does not rule out no rate difference at that confidence level. Its width also indicates that the estimate is not exact. The result supports a range of plausible rate ratios rather than one certain value.

The two arm-specific rate estimates were 0.97 per patient-year for tiotropium, with a 99% confidence interval from 0.9 to 1.03, and 0.9 per patient-year for the combination, with a 99% confidence interval from 0.84 to 0.96. Arm-specific intervals describe uncertainty in each estimated rate; they are not a substitute for the interval around the between-group comparison. In particular, comparing overlap between separate arm intervals is not the same as testing the difference between groups.

The sponsor’s comparison interval and the recalculated interval differ substantially. The recalculated unadjusted interval, from 0.387 to 2.222, is much wider and was derived using a simple approach from posted summary statistics. The registry flags this discrepancy. The sponsor’s model-based analysis takes precedence, while the recalculation illustrates how conclusions about precision can depend on the statistical model and available information.

Confidence intervals do not describe the range of individual participants’ outcomes, and they do not guarantee that the true effect lies within a particular realized interval. They express uncertainty under the analysis method. The registry record does not report enough detail to assess all sources of uncertainty, including missing-data handling and model diagnostics.

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 illustrations use assumptions stated in the registry record: 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. For the rate endpoint, the figures are participants per arm. For time-to-event outcomes, the corresponding planning figures are total events; the other illustrations give participants per arm.

The 80% power column means the number of participants per arm that a hypothetical future study would require, under those assumptions, to have an 80% chance of detecting the chosen effect if that effect were the true one. The 90% power column uses a higher chance of detecting that effect and therefore generally calls for a larger planning sample. These are design-planning quantities, not counts of people observed in DYNAGITO.

The rows describe planning for 100%, 75%, and 50% of the observed effect. As the effect targeted for detection becomes smaller, more participants are needed to distinguish it from random variation under the same assumptions. The figures are particularly large for the primary rate comparison because the observed effect used for planning is modest relative to the event-rate variability assumed by the calculation.

These figures are planning illustrations based on the observed effect, not observed power. The registry record does not report the trial’s original sample-size justification or the assumptions used to set its planned enrollment. A sample-size curve represents how the planning requirement changes as the target effect changes; it does not show a new estimate of treatment effect or alter the sponsor’s analysis.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 0.9700; treatment rate λ₁ = 0.9000 events per patient-year; follow-up T = 0.00 years.
2. n = (1.96 + 0.842)² × (1/0.9700 + 1/0.9000) / (0.00 × [ln(0.928)]²) = 1,094,577.3, rounded up to 1,094,578 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
lambda0 <- 0.97                      # control rate, events per patient-year
lambda1 <- 0.9                      # treatment rate
tt      <- 0.0027378507871321                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(2296138)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 1,094,578 (80% power), 1,465,329 (90% power)
 75% of observed effect: n per arm = 1,927,191 (80% power), 2,579,961 (90% power)
 50% of observed effect: n per arm = 4,294,829 (80% power), 5,749,557 (90% power)
Simulated power, Poisson counts, n = 1,094,578 per arm: 0.800
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.633

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis used a negative binomial model and reported a rate ratio of 0.93, with a 99% confidence interval from 0.85 to 1.02 and p = 0.050. This is the trial’s own reported analysis and takes precedence over the simple recalculation. The sponsor’s estimate is based on a model for the event-rate outcome, whereas the recalculation uses posted summary statistics in an unadjusted Poisson approach.

The recalculated rate ratio is 0.928, with a confidence interval from 0.387 to 2.222 and p = 0.867. The estimates point in a similar direction numerically, but the uncertainty and p-value differ considerably. The registry record explicitly flags a discrepancy, so the recalculated result should be read as a sensitivity illustration, not as a replacement or correction of the sponsor’s result.

The record also lists additional sponsor-reported rate-ratio analyses for the primary outcome, including estimates of 0.89, 0.91, and 0.89 with 95% confidence intervals. Their intervals and p-values vary. The registry record does not explain the analysis populations or other distinctions among these entries, so their differences should not be attributed to a particular modeling choice or subgroup. The 99% result is the entry identified as the primary analysis in the posted results.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the primary and secondary hypothesis tests were adjusted for multiplicity, or whether a prespecified testing hierarchy was used. This is important because the record lists multiple outcomes and analyses. When several hypotheses are tested, the chance of at least one apparently notable result can increase. A prespecified procedure can control that risk, but the procedure used in this trial is not reported in the registry record.

The primary result includes a 99% confidence interval, while several other reported analyses use 95% intervals. The record does not explain the rationale for the confidence levels or how they relate to any overall error-control plan. The p-values therefore should be interpreted alongside the reported intervals and with caution about unreported multiplicity handling. The nominal primary p-value alone does not establish the study-wide strength of evidence.

The registry identifies the treated set as the primary population: randomized patients documented to have taken at least one dose of trial medication. It does not report the number randomized in each group separately from the treated set, the handling of participants excluded from that set, or whether an intention-to-treat analysis was also conducted. Details about missing outcome data, imputation, censoring, and sensitivity analyses are not reported in the registry record.

Those omissions do not show that such methods were absent from the full study documentation. They mean only that the registry record does not permit an independent assessment of them. The record also does not report interim analyses, stopping rules, or the trial’s original sample-size justification. Those aspects should remain unknown rather than being inferred from the final results or the posted planning illustrations.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

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 (10.3%), pneumonia (3.7%), respiratory failure (1.1%), acute respiratory failure (0.6%), cardiac failure (0.6%).

The registry lists serious adverse events affecting 862 participants in the tiotropium group and 810 in the combination group. It lists other adverse events affecting 1786 and 1770 participants, respectively, and deaths of 98 and 92. The at-risk counts recorded for these groups were 3941 and 3939. These are posted counts and do not, by themselves, establish whether an event was caused by study treatment.

The leading serious adverse-event terms listed include chronic obstructive pulmonary disease (10.3%), pneumonia (3.7%), respiratory failure (1.1%), acute respiratory failure (0.6%), cardiac failure (0.6%), and atrial fibrillation (0.5%). The registry record does not specify the denominator or detailed coding context for these percentages in the posted summary. The terms should therefore be read as reported categories, not as a complete description of safety outcomes.

Adverse-event counts are descriptive. A comparison of counts alone does not account for event severity, duration of exposure, recurrent events, or other differences in follow-up. The registry record does not provide enough detail to assess causality, exposure-adjusted risks, or the statistical methods used for safety comparisons.

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

The results describe a randomized comparison of two inhaled treatment regimens in patients with severe to very severe COPD. The primary endpoint was an annualised rate of moderate to severe exacerbations during actual treatment. The sponsor’s estimated rate ratio was below 1, indicating a lower estimated rate in the combination group relative to tiotropium in that analysis. Its 99% confidence interval nevertheless includes 1, so the posted primary estimate remains compatible with no rate difference at that confidence level.

This is not the same as concluding that the treatments are identical. A confidence interval that includes the no-difference value indicates uncertainty; it does not establish equivalence. The registry record does not report an equivalence or non-inferiority design. Nor does the result establish the size of an effect for every participant: the primary result is a group-level rate comparison.

The secondary results provide related information about whether participants experienced events and about hospitalisation, but they use different outcome definitions and analyses. Their estimates do not remove uncertainty in the primary comparison. The sponsor’s analysis should be distinguished from the simple recalculation, which is substantially less precise and does not reproduce the reported model-based analysis.

The findings also do not establish that any observed difference is clinically important. The registry record does not provide a threshold for clinical importance. These results describe the estimates and statistical uncertainty recorded for this trial; they do not provide medical advice or establish how results would apply to patients outside the studied population.

18. Why This Trial Matters Statistically

This trial illustrates why the statistical form of an endpoint matters. Moderate to severe exacerbations can recur, and participants contribute different amounts of treatment exposure. The primary rate endpoint incorporates exposure time and concerns event frequency, while the secondary binary endpoint asks whether a participant experienced at least one event. Those outcomes can tell different parts of the clinical story and require different analyses.

The record also illustrates the importance of using the study’s own analysis when available. The sponsor used a negative binomial model for the primary endpoint, whereas the simple recalculation uses an unadjusted Poisson approach and yields substantially different uncertainty. Event-count analyses depend on modeling choices, including how extra variability is handled. Summary statistics alone may not contain enough information to reproduce a trial analysis.

Finally, a point estimate and its precision must be read together. The primary rate ratio is below 1, but its 99% confidence interval includes 1. A single p-value does not replace the interval, and unreported multiplicity procedures limit interpretation of borderline statistical evidence. The trial is therefore a useful example of distinguishing numerical direction, statistical uncertainty, model dependence, and the limits of conclusions from registry results.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The registry record does not report the full statistical analysis plan, including multiplicity control, the role of each listed analysis, or why different confidence levels appear across reported results. This limits the ability to identify which results were confirmatory and to interpret individual p-values within the study-wide testing strategy.

Important analysis details are also not reported, including model covariates, diagnostics, missing-data methods, censoring rules, and sensitivity analyses. The primary population is defined as the treated set, but the registry does not provide enough information to compare it with all randomized participants or to assess exclusions from the treated set. The original sample-size rationale and any interim analyses are not reported in the registry record.

The posted primary analysis and the simple recalculation differ substantially in precision. The sponsor’s negative binomial result takes precedence, but the discrepancy cautions against reconstructing a model-based event-rate comparison from summary data. The registry record does not supply enough detail to explain all differences among the multiple reported primary analyses.

The safety summary lists event counts and selected serious-event terms, but does not provide full exposure-adjusted comparisons or detailed attribution information. The record’s limited description of the serious-event percentages also prevents a complete assessment of their denominators. These limitations concern what can be assessed from the registry record and do not establish what was or was not reported in other study documents.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Comparing the Efficacy of Tiotropium + Olodaterol (5/5 µg) Fixed Dose Combination (FDC) Over Tiotropium 5µg in Reducing Moderate to Severe Exacerbations in Patients With Severe to Very Severe Chronic Obstructive Pulmonary Disease. — NCT02296138.
• Registry record last updated 2018-06-04; status last verified 2018-05.
• Results first posted 2018-06-04.
• 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

DYNAGITO was a completed Phase 3 randomized, double-blind, parallel-group study sponsored by Boehringer Ingelheim. It compared once-daily tiotropium plus olodaterol 5 μg/5 μg with tiotropium 5 μg in patients with severe to very severe COPD. Both regimens used the Respimat inhaler. The registry reports enrollment of 7903.

The primary outcome was the annualised rate of moderate to severe COPD exacerbations per patient-year during actual treatment, up to 361 days. The sponsor’s negative binomial analysis reported a rate ratio of 0.93, with a 99% confidence interval from 0.85 to 1.02 and p = 0.050. The interval includes 1. A simple unadjusted recalculation differs substantially, and the sponsor’s analysis takes precedence.

Secondary outcomes addressed exacerbation occurrence, hospitalisation, and all-cause mortality. The registry record does not report the full multiplicity plan, missing-data methods, or original sample-size justification.