Efficacy Study of Nebulized TD-4208 for Chronic Obstructive Pulmonary Disease (COPD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy Study of Nebulized TD-4208 for Chronic Obstructive Pulmonary Disease (COPD) (NCT02459080), a randomized phase 3 study. The primary outcome is Change From Baseline in Trough FEV1 on Day 85.

2. Clinical Question

The statistical question is about the difference between each active-treatment arm and placebo in the recorded endpoint, not about whether an individual participant’s lung function changed. The registry lists results for both TD-4208 doses and placebo. It also lists other lung-function and symptom-related outcomes, including trough FEV1 across Days 15 to 85, peak FEV1 after the first dose, rescue medication use, rescue-free periods, and a respiratory questionnaire outcome. Those additional measures can provide context about the primary result, but they are not substitutes for it.

3. Trial Design

This was a Phase 3, randomized, double-blind, placebo-controlled, parallel-group study of nebulized TD-4208 in people with COPD. The registry describes triple masking. The planned treatment period was 12 weeks. The trial was marked completed, with a recorded start of 2015-09 and primary completion in 2016-08. Enrollment was 619.

The registry lists three arms: TD-4208 at 88 mcg, TD-4208 at 175 mcg, and placebo. Random allocation and a parallel-group model mean participants were assigned to a treatment group and the listed groups were compared. Double-blind and triple-masked describe the registry’s masking classifications; which particular parties were masked is not reported in the registry record.

The primary outcome was change from baseline in trough FEV1 on Day 85, measured in mL. Its stated analysis population was the ITT analysis set. The primary arm summaries report 161 for TD-4208 at 88 mcg, 156 for TD-4208 at 175 mcg, and 146 for placebo. These are the counts accompanying the primary endpoint summaries, not a replacement for the registry’s overall enrollment figure. The reasons for differences between endpoint counts and enrollment, including any exclusions or unavailable measurements, are not reported in the registry record.

The record also lists secondary outcomes over different timeframes, with some summaries using different arm counts from the primary endpoint. It does not give the original sample-size justification, the trial’s full statistical analysis plan, or detailed analysis procedures. The registry identifies the trial’s design features and posted outcome summaries, but those details alone do not establish how every operational or analytic decision was made.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) analysis set

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 Change From Baseline in Trough FEV1 on Day 85, measured over Day 85.

The primary endpoint is change from baseline in trough FEV1 on Day 85, expressed in mL. FEV1 is the amount of air a person can forcefully exhale in the first second of a breath test. A trough measurement refers to a measurement at a low point in the dosing interval, rather than the response measured soon after a dose. Change from baseline expresses the Day 85 measurement relative to the participant’s starting measurement.

FEV1 is used as a continuous lung-function measure. A continuous outcome retains information about the size and direction of measured changes, rather than reducing the outcome to categories such as improved or not improved. Comparing the average change in each randomized arm with the placebo arm addresses whether their recorded changes differed over the trial period. The primary endpoint is a specified measurement at a specified time, which helps focus interpretation on the main registered question rather than selecting among several outcomes after seeing results.

The registry reports least-squares means and standard errors for the primary endpoint. A least-squares mean is a model-based mean; the model and covariates used to obtain it are not described in the registry record. Standard error reflects the estimated precision of a mean, rather than the spread of individual participant measurements. The reported primary endpoint summaries therefore describe estimated group-level changes and their uncertainty, not the range of individual responses.

The record does not report a threshold for a clinically important difference in FEV1. Statistical evidence of a difference between group summaries does not by itself determine how important that difference is to participants or how it relates to other clinical outcomes.

7. Results Posted in the Registry

• TD-4208-1: mean 59.81 versus -19.41 on control; difference 79.22 (95% CI 35.95 to 122.49), standardized effect d = 0.41; z-test p = <0.001.
• TD-4208-2: mean 126.85 versus -19.41 on control; difference 146.26 (95% CI 102.60 to 189.92), standardized effect d = 0.76; 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.

Summary of Trough FEV1 Overall Treatment Effect From Day 15 to Day 85

• 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:
  • TD-4208-1: mean 73.00 versus -30.80 on control; difference 103.80 (95% CI 95.10 to 112.50), standardized effect d = 2.36; z-test p = <0.001.
  • TD-4208-2: mean 124.80 versus -30.80 on control; difference 155.60 (95% CI 146.76 to 164.44), standardized effect d = 3.54; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for TD-4208-1 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for TD-4208-2 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Summary of Change From Baseline to Peak FEV1 After First Dose

• 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:
  • TD-4208-1: mean 218.14 versus 91.79 on control; difference 126.35 (95% CI 99.31 to 153.39), standardized effect d = 0.89; z-test p = <0.001.
  • TD-4208-2: mean 224.46 versus 91.79 on control; difference 132.67 (95% CI 105.36 to 159.98), standardized effect d = 0.94; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for TD-4208-1 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for TD-4208-2 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Summary of Rescue Medication Use: Puffs Per Day

• 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:
  • TD-4208-1: mean 2.26 versus 2.72 on control; difference -0.46 (95% CI -1.13 to 0.21), standardized effect d = -0.13; z-test p = 0.175.
  • TD-4208-2: mean 2.27 versus 2.72 on control; difference -0.45 (95% CI -1.12 to 0.22), standardized effect d = -0.13; z-test p = 0.190.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TD-4208-1 and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TD-4208-2 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary question across other lung-function measures, time periods, and symptom-related measures. The posted summaries show positive estimated comparisons against placebo for trough FEV1 over Days 15 to 85 and for peak FEV1 after the first dose. Rescue medication use has negative estimated comparisons, while its reported unadjusted confidence intervals span zero. Taken together, the pattern is not uniform across all kinds of outcome, but the lung-function summaries point in a direction consistent with the primary endpoint.

These outcomes relate to, but do not duplicate, the primary result. The primary endpoint concerns change from baseline in trough FEV1 on Day 85. An overall trough FEV1 summary across Days 15 to 85 uses a different timeframe; peak FEV1 after the first dose measures a different point in the response; and rescue medication use reflects a different measure. Similarity across related outcomes can add context, but differences in measurement and timing make them unsuitable as interchangeable replications of the primary endpoint.

The registry also names rescue-free periods and a respiratory questionnaire responder outcome, but it does not post numeric results for those outcomes in the available secondary summaries. Their results should not be inferred from the other secondary measures.

Unadjusted secondary findings carry less weight because several outcomes and comparisons create multiple opportunities for apparently notable results. The registry record does not report whether a multiplicity adjustment or hierarchy was prespecified. Secondary results can be informative and help describe the breadth of the recorded pattern, but without a reported testing strategy they should be treated as exploratory context rather than independent confirmation of the primary result. The absence of a reported adjustment does not prove that none was used in the trial’s full analysis; it means that the registry record does not document one.

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

• Summary of Trough FEV1 Overall Treatment Effect From Day 15 to Day 85
• Summary of Change From Baseline to Peak FEV1 After First Dose
• Summary of Rescue Medication Use: Puffs Per Day
• Percentage of Albuterol Rescue-free 24-hour Periods
• St. George's Respiratory Questionnaire (SGRQ) Proportion of Responders on Day 85

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous, so it is summarized with group means rather than event counts. The posted parameter is a least-squares mean and its accompanying dispersion measure is a standard error. A mean gives a measure of the group’s average change. A standard error describes uncertainty in an estimated mean; it is not the standard deviation of individual measurements and should not be read as the amount of variation among participants.

What does a mean difference represent?

A mean difference compares the average outcome in one arm with the average outcome in the reference arm. A positive value in the primary comparison means the posted mean change was higher in the TD-4208 arm than in placebo. The primary contrasts are 79.22 mL for 88 mcg versus placebo and 146.3 mL for 175 mcg versus placebo. These estimates are recalculated unadjusted contrasts from the posted group summaries. They are not adjusted for factors that are not included in those summaries.

The record provides arm-level least-squares means, but does not identify a model or covariates used to calculate them. It also does not list sponsor-reported analyses for the outcomes discussed. Since the contrast calculations are simple and unadjusted, they can help describe the posted summaries, but they do not reproduce an undocumented trial model or replace the sponsor’s own analysis if it is available elsewhere.

How should a confidence interval be read?

A confidence interval describes uncertainty around an estimated contrast. In general, a narrower interval indicates greater precision, while a wider interval leaves more uncertainty about the size of the difference. For the primary endpoint, the recalculated 95% confidence intervals are 35.95 to 122.5 mL for 88 mcg versus placebo and 102.6 to 189.9 mL for 175 mcg versus placebo. Both intervals lie above zero. This is consistent with the small unadjusted p-values reported for those comparisons, but neither interval expresses the range of individual participant outcomes.

A confidence interval is not a guarantee that the true value falls within its limits, nor does it establish clinical importance. The registry does not report a threshold for a clinically important FEV1 difference. The interval’s interpretation also depends on the statistical method used to construct it; the detailed method for the trial’s own analyses is not reported in the registry record.

What does a p-value say?

A p-value assesses how compatible the observed data are with a specified null hypothesis under a statistical model. A small p-value is evidence against that null under the stated analysis assumptions; it is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The posted primary comparison values are p < 0.001 for both TD-4208 doses versus placebo. They are unadjusted recalculations, not evidence that multiple testing was accounted for.

Because multiple outcomes and comparisons appear in the registry, the chance of finding at least one apparently unusual result can increase when many hypotheses are tested. A multiplicity strategy can address this issue by controlling the interpretation or error rate across a family of tests. Whether the trial prespecified such a strategy, and what that strategy might have been, is not reported in the registry record. The unadjusted p-values should therefore be read as comparison-specific results, not as multiplicity-adjusted conclusions.

Why does over-dispersion matter?

Over-dispersion is a general issue in count outcomes: observed counts can vary more than a simple count model expects. A model that assumes too little variability can underestimate uncertainty and make evidence appear stronger than it is. The primary endpoint is a continuous FEV1 measure rather than a count, so this particular count-data concern is not central to its mean comparison. It can matter in general when analysing outcomes such as event counts, where the choice of variance model affects standard errors and intervals. The registry record does not provide the modelling details needed to assess count-data methods for other outcomes.

What can be inferred from the analysis population?

The primary endpoint is identified as using an ITT analysis set. In general, an ITT approach aims to retain participants in their randomized groups, but the registry does not define the set or explain how unavailable Day 85 measurements were treated. The endpoint summaries show arm counts of 161, 156, and 146; those figures do not on their own disclose why some enrolled participants are not represented in the outcome summaries. Missing-data methods and sensitivity analyses are not reported in the registry record.

The secondary summaries use their own recorded arm counts, and these vary by outcome. Such differences may arise for several reasons, but the reasons are not reported in the registry record and should not be guessed. Without details on missingness and analysis populations for each secondary endpoint, comparisons across outcomes should be understood as summaries of the respective posted analyses, not as evidence that every outcome used an identical set of participants or method.

Finally, statistical significance and estimation are related but distinct. The estimated difference communicates the direction and size of the group contrast; the confidence interval communicates its precision; and the p-value assesses compatibility with a null hypothesis under a model. None of these alone answers whether a result is clinically meaningful, generalizable to all people with COPD, or robust to analysis choices that the registry does not describe.

11. Confidence Intervals and Precision

The primary contrasts are estimated with some uncertainty. For 88 mcg versus placebo, the recalculated mean difference is 79.22 mL and the 95% confidence interval ranges from 35.95 to 122.5 mL. For 175 mcg versus placebo, the estimate is 146.3 mL and the interval ranges from 102.6 to 189.9 mL. Both intervals are above zero, but each spans a range of possible contrast values rather than identifying a single exact effect.

The standard errors attached to the primary arm summaries are 15.1 mL for 88 mcg, 15.39 mL for 175 mcg, and 16.11 mL for placebo. A standard error describes precision of an estimated mean, not the spread of individual participant outcomes. Confidence intervals for the contrasts combine uncertainty from the groups being compared; they should not be inferred simply by looking at one arm’s standard error in isolation.

Precision is also different from clinical importance. The registry does not report a threshold that would distinguish a clinically important FEV1 change from a smaller one. The intervals show that the recalculated contrast estimates are imprecise to some degree, while remaining above zero under the stated calculation. They do not establish how participants experienced the changes or whether the estimates would be similar in another population or setting.

The intervals are based on simple unadjusted recalculations from posted summary statistics, not a documented reproduction of the trial’s full analysis. Details of the sponsor’s analysis model and interval method are not reported in the registry record. The interval endpoints should therefore be interpreted as precision estimates for these recalculated comparisons, with that limitation in mind.

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 report participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each illustration, the assumed effect is a stated fraction of the observed effect: 100%, 75%, or 50%. These are planning assumptions for an illustration based on the observed estimate; the trial’s own original sample-size assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm the illustration estimates would be needed to have an 80% chance of detecting the specified effect under its assumptions, if that effect and model assumptions were correct. The 90% power column uses a higher target chance of detection and therefore generally calls for more participants for the same effect. The entries are planning quantities, not descriptions of the trial’s enrollment or endpoint counts.

Smaller assumed effects require more participants because a smaller contrast is harder to distinguish from random variation. For example, each comparison’s illustration gives larger per-arm requirements when the assumed effect is 50% of the observed effect than when it is 100%. This dependence on the observed estimate is important: if the original observed effect is unusually large or small, the resulting illustrations can be misleading as forecasts for a new study.

This is not observed power. It is a planning illustration under stated assumptions, not a retrospective measure of how likely the completed trial was to detect its observed result. The trial’s own design justification and original power calculation 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 = 79.220; pooled standard deviation σ = 193.014.
2. n = 2 × (1.96 + 0.842)² × 193.014² / 79.220² = 93.2, rounded up to 94 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 <- 79.22                      # observed difference in means
sigma <- 193.013878129077                     # 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(2459080)
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 = 94 (80% power), 125 (90% power)
 75% of observed effect: n per arm = 166 (80% power), 222 (90% power)
 50% of observed effect: n per arm = 373 (80% power), 499 (90% power)
power.t.test: 94.2 
Simulated power at n = 94 per arm: 0.796 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes, and the posted results include more than one comparison with placebo. Testing many outcomes or contrasts can increase the chance that at least one result appears statistically notable by chance. A prespecified multiplicity plan can address that concern by setting priorities among endpoints or adjusting how evidence is evaluated. The multiplicity procedure, if any, is not reported in the registry record. The recalculated comparison p-values are unadjusted, so they do not account for a family of tests.

The primary endpoint population is identified as the ITT analysis set, but the record does not give a detailed definition of that set. It does not explain how participants without a Day 85 measurement were handled, whether any imputation was used, or whether sensitivity analyses were conducted. The reported endpoint counts differ across outcomes. Those differences are visible in the summaries, but the reasons are not reported in the registry record.

Missing-data processes can affect the interpretation of group comparisons if the availability of measurements is related to treatment or outcome. That is a general statistical concern, not a finding that missingness biased this trial. Without counts and reasons for missing measurements, plus the analysis methods used to address them, the extent of any effect cannot be assessed from the record.

The registry does not report the detailed statistical analysis plan, the original model specifications, or the sponsor’s outcome analyses. It also does not provide enough information to establish whether the posted mean summaries account for baseline factors or other covariates. These omissions do not invalidate the numerical summaries, but they limit how fully the recalculated comparisons can be interpreted as representing the trial’s prespecified inferential analysis.

Finally, the registry names secondary outcomes for which numeric results are not included in the posted secondary summaries. No result should be inferred for an outcome simply because it was listed in the study record. The resulting picture is incomplete with respect to the full set of planned endpoints and analysis decisions.

15. 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 2% 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 (2.0%), bronchiectasis (0.5%), hypoxia (0.5%), chest pain (0.5%), non-cardiac chest pain (0.5%).

The registry lists serious adverse events among participants at risk in each arm. Serious adverse events affected 10 of 212 participants in the 88 mcg arm, 10 of 198 in the 175 mcg arm, and 14 of 209 in the placebo arm. The reported deaths were 0, 0, and 1, respectively. These are descriptive counts; they do not by themselves establish a causal relationship to treatment or provide a complete comparison of risk.

The registry also reports other adverse events affecting 51 of 212 participants in the 88 mcg arm, 46 of 198 in the 175 mcg arm, and 51 of 209 in the placebo arm. The serious-event terms listed most prominently include chronic obstructive pulmonary disease at 2.0%, followed by bronchiectasis, hypoxia, chest pain, non-cardiac chest pain, and acute myocardial infarction, each at 0.5%.

These counts should be read alongside the study’s duration, the number at risk in each group, and the event definitions used. The registry does not provide enough detail to judge event timing, recurrence, severity grades, attribution, or statistical comparisons. Differences in counts are descriptive and should not be treated as proof that one arm had higher or lower treatment-related risk.

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

The primary result describes a difference in average change in trough FEV1 at Day 85 between each TD-4208 arm and placebo. The posted arm summaries and recalculated unadjusted contrasts show higher mean changes in both TD-4208 arms than in placebo, with the reported 95% confidence intervals above zero and p-values below 0.001. This is a statistical description of the recorded group-level outcome in the analyzed participants.

That finding does not, by itself, establish how important the estimated differences are to patients. The registry does not report a clinical-importance threshold for FEV1, and the group averages do not show how much participants’ individual measurements varied or how many participants experienced a meaningful change. The primary result also does not answer every question about COPD symptoms, daily function, exacerbations, or long-term outcomes.

The result is specific to the trial population, treatment arms, study period, and endpoint definition recorded in the registry. The study was conducted over 12 weeks, and the primary endpoint was assessed at Day 85. The registry does not establish that the estimates apply to people outside the studied population or to periods beyond the recorded trial. It also does not report the full analysis plan, detailed missing-data methods, or multiplicity strategy needed to evaluate all analytic choices.

Related secondary lung-function summaries have a pattern consistent with the primary comparison, while rescue medication use does not show the same clear separation in the unadjusted recalculations. Secondary outcomes have different meanings and their unadjusted analyses deserve more cautious interpretation, especially where multiple outcomes were considered.

Statistical evidence is not the same as a treatment recommendation. These results alone do not determine the balance of benefits and risks for an individual, establish long-term safety, or answer whether a treatment should be used. They report what the registry’s posted outcome summaries indicate and the limits of the available statistical detail.

17. Why This Trial Matters Statistically

This trial illustrates why the endpoint, contrast, and uncertainty all matter when reading a clinical study. A group mean change alone does not answer the comparative question; the placebo-referenced contrast shows how the active-arm summary differs from the comparator. The confidence intervals then make clear that an estimated contrast is not an exact value, even when the interval lies above zero and the unadjusted p-value is small.

It also demonstrates why statistical significance and clinical importance should be kept separate. The primary comparisons have p < 0.001, but the registry does not provide a threshold for a clinically important FEV1 difference. A p-value cannot supply that missing clinical interpretation. The magnitude and precision of the estimate, the outcome’s relevance, and the broader evidence all matter, while the registry record does not supply every element needed for that broader judgment.

The different secondary outcomes show how interpretation can vary with the measure and timeframe. Related lung-function summaries have positive contrasts, while rescue medication results are less conclusive in the unadjusted recalculations. This helps illustrate why secondary outcomes provide context but do not all carry the same evidential weight as a prespecified primary endpoint, particularly when a multiplicity plan is not documented.

Finally, registry results make the limits of available reporting visible. The primary analysis population is named, but missing-data procedures, model details, original sample-size justification, and multiplicity handling are not reported. The distinctions between trial design details, posted estimates, and recalculated comparisons are essential to avoid treating a transparent summary as a substitute for a complete statistical analysis plan.

18. 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.

Several limitations are specific to the available record. Although the primary outcome is identified as an ITT analysis, the record does not define the analysis set in detail or describe how unavailable endpoint measurements were handled. Arm counts differ between the primary and secondary summaries, but reasons for those differences are not reported. Without missingness counts, reasons, and sensitivity analyses, it is not possible to assess how robust the estimates are to missing outcome data.

The comparisons discussed are simple unadjusted recalculations from posted summary statistics. The registry does not list the sponsor’s reported analyses or enough model detail to reproduce them. It does not say whether the trial’s own analyses adjusted for baseline variables or other covariates. The recalculated contrasts should therefore not be treated as a complete restatement of the trial’s planned analysis.

The record does not report the trial’s original sample-size assumptions, the statistical analysis plan, or a multiplicity procedure. Several outcomes and comparisons are listed, but the available results do not establish how testing was prioritized or controlled across them. Some named secondary outcomes have no numeric results in the posted summaries, so the available secondary picture is incomplete.

The registry does not report a clinical-importance threshold for the primary endpoint. Nor do the posted summaries provide individual participant distributions, which would help describe heterogeneity in response. The study’s 12-week period and Day 85 primary measurement also limit what can be said from these results about outcomes beyond that period.

These are reporting limitations, not proof that a particular analytic choice was incorrect. They define what can and cannot be evaluated from the registry record alone.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy Study of Nebulized TD-4208 for Chronic Obstructive Pulmonary Disease (COPD) — NCT02459080.
• Registry record last updated 2022-02-24; status last verified 2022-02.
• Results first posted 2018-12-31.
• 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.

22. Record Summary

The registry record describes a completed Phase 3 randomized, double-blind, placebo-controlled parallel-group study of nebulized TD-4208 in COPD. Enrollment was 619, and the study period was 12 weeks. The primary outcome was change from baseline in trough FEV1 on Day 85, measured in mL in the ITT analysis set.

Posted primary summaries show higher mean changes in both TD-4208 arms than in placebo. Recalculated unadjusted comparisons are 79.22 mL for 88 mcg versus placebo and 146.3 mL for 175 mcg versus placebo; both have p < 0.001. Secondary summaries show varied patterns across related and symptom-related measures. Serious adverse-event counts and deaths are also recorded.

The registry does not report the full analysis plan, multiplicity procedure, detailed missing-data handling, original sample-size justification, or clinical-importance threshold. The results support a statistical description of the recorded comparisons, with those limits in mind.