RETHINC: REdefining THerapy In Early COPD for the Pulmonary Trials Cooperative: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for RETHINC: REdefining THerapy In Early COPD for the Pulmonary Trials Cooperative (NCT02867761), a randomized phase 3 study. The primary outcome is Proportion (Percentage) of Individuals Who Experience a 4 Unit Improvement in St. George's Respiratory Questionnaire (SGRQ) at 12 Weeks and do Not Meet Criteria for Treatment Failure During the 12 Week Treatment Period.

2. Clinical Question

The registry’s stated hypothesis was that symptomatic current and former smokers with normal-range spirometric values would derive symptomatic benefit from long-acting bronchodilator therapy. The primary outcome combines a change in a patient-reported respiratory health status score with a treatment-failure condition. It therefore asks about achieving a specified improvement while avoiding the registry-defined worsening that would prompt additional treatment. The posted results compare the proportion meeting this combined outcome in the indacaterol/glycopyrrolate and placebo groups.

This question is specific to the selected population, treatment regimen, follow-up period, and outcome definition. It does not by itself address longer-term outcomes or people outside the described spirometric and smoking criteria. Further eligibility details are not reported in the registry record.

3. Trial Design

RETHINC is registered as a phase 3, randomized, quadruple-masked, parallel-group trial sponsored by the University of Michigan. The registry reports enrollment of 780 and a completed study. The recorded start date is 2017-08-29 and the primary completion date is 2021-07-07. Randomization assigns participants to one of two groups, and the parallel design means the groups receive their assigned regimen over the same study period rather than switching between treatments.

The active group received indacaterol/glycopyrrolate 27.5/15.6 mcg inhaled twice daily for 12 weeks. The comparison group received placebo 27.5/15.6 mcg inhaled twice daily for 12 weeks. The registry labels masking as quadruple, but the specific roles of the masked parties are not reported in the registry record. The method of sequence generation, allocation concealment, and any stratification factors are also not reported in the registry record.

For the primary outcome, the posted group counts are 128 participants meeting the outcome among 227 assessed in the indacaterol/glycopyrrolate group, and 144 among 244 in the placebo group. These outcome denominators are distinct from the total enrollment figure. The primary outcome description notes exclusions and missing final-visit SGRQ information, but the full text of its population description is incomplete in the registry record. The safety results use separate at-risk group counts. These differences in denominators matter: outcome and safety summaries describe the participants included in those specific summaries, not necessarily every enrolled participant.

The registry lists 14 outcome measures and 12 analyses. Its listed secondary outcomes include patient-reported measures and lung-function measures. Details of the trial’s original sample-size justification, prespecified analysis plan, and interim analyses are not reported in the registry record. The planning illustrations associated with the posted results are separate from the trial’s original design assumptions.

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: Of the 780 consented, 242 were screen fails and 3 dropped out before randomization, so 535 were randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: In the treatment arm, 5 subjects had primary efficacy assessment \>=4 weeks after the last visit that were not included in the mITT (233 - 5 = 228). One additional subject was missing SGRQ at final visit (228 - 1 = 227). In the placebo arm, 5 subjects had primary efficacy assessment \>=4 weeks after the last visit that were not included in the mITT (248 - 5 = 243). An additional person did not complete final visit but had treatment failure so are still included in mITT (243 + 1 = 244).

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 Proportion (Percentage) of Individuals Who Experience a 4 Unit Improvement in St. George's Respiratory Questionnaire (SGRQ) at 12 Weeks and do Not Meet Criteria for Treatment Failure During the 12 Week Treatment Period, measured over Baseline and 12 weeks.

The primary endpoint is the proportion of participants with a 4-unit improvement in the St. George’s Respiratory Questionnaire (SGRQ) at 12 weeks who did not meet treatment-failure criteria during the 12-week treatment period. The registry identifies 4 units as the minimum clinically important difference. SGRQ scores range from 0 to 100, with 0 indicating low symptoms or feeling better and 100 indicating high symptoms or feeling worse.

Treatment failure is defined in the registry as an increase in lower respiratory symptoms necessitating treatment with an active, long-acting inhaled bronchodilator, corticosteroids, or antibiotics. The endpoint therefore requires both the specified SGRQ improvement and the absence of this treatment failure. A participant who improves on the questionnaire but meets the failure definition does not satisfy the combined outcome.

A responder proportion is useful because it describes how many participants met a defined outcome, rather than only reporting an average score change. The threshold also gives the outcome a patient-centered interpretation tied to a change the registry regards as clinically important. However, reducing score changes to a responder category discards information about the size and distribution of changes, and the combined endpoint reflects both questionnaire response and treatment-failure status. The registry’s endpoint definition does not, on its own, establish how missing scores or other analysis-population issues were handled in the sponsor’s analysis.

7. Results Posted in the Registry

• Indacaterol/Glycopyrrolate: 56.4% (128/227) versus 59.0% (144/244) on control; risk difference -2.6 percentage points (95% CI -11.6 to 6.3), risk ratio 0.96 (0.82–1.12); unadjusted two-proportion z-test p = 0.564.

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.

Proportion of Individuals With a 2 Unit Improvement in CAT Without Treatment Failure

• 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:
  • Indacaterol/Glycopyrrolate: 74.4% (169/227) versus 68.0% (166/244) on control; risk difference 6.4 percentage points (95% CI -1.7 to 14.6), risk ratio 1.09 (0.98–1.23); unadjusted two-proportion z-test p = 0.125.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Indacaterol/Glycopyrrolate and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Individuals With a 1 Unit Improvement in the BDI/TDI Without Treatment Failure

• 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:
  • Indacaterol/Glycopyrrolate: 36.4% (80/220) versus 34.2% (80/234) on control; risk difference 2.2 percentage points (95% CI -6.6 to 11.0), risk ratio 1.06 (0.83–1.36); unadjusted two-proportion z-test p = 0.628.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Indacaterol/Glycopyrrolate and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Individuals With Both a 4 Unit Improvement in SGRQ and a 1 Unit Improvement in BDI/TDI Without Treatment Failure

• 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:
  • Indacaterol/Glycopyrrolate: 25.0% (55/220) versus 25.6% (60/234) on control; risk difference -0.6 percentage points (95% CI -8.6 to 7.4), risk ratio 0.98 (0.71–1.34); unadjusted two-proportion z-test p = 0.875.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Indacaterol/Glycopyrrolate and the control. The interval gives the range of effects that remain compatible with the data.

The posted binary secondary outcomes show a mixed pattern rather than a consistent separation across measures. The CAT responder comparison points toward a higher proportion in the indacaterol/glycopyrrolate group, while the BDI/TDI responder and combined SGRQ/BDI/TDI responder comparisons are much closer between groups. Their unadjusted p-values are 0.125, 0.628, and 0.875, respectively. These results do not provide a consistent secondary-outcome pattern that overturns the primary result.

Secondary measures can help describe different aspects of symptoms and respiratory health. They may support interpretation of the primary endpoint when their definitions and directions are considered together, but they are not independent confirmations simply because several are reported. The primary endpoint is the registry’s central outcome, and the secondary findings should be interpreted in relation to it rather than treated as substitutes.

Unadjusted secondary results carry less weight when many outcomes are examined. General statistical explanation: testing multiple outcomes increases the chance that at least one result appears unusual by chance, even when there is no underlying difference. Adjusting for multiplicity or following a prespecified hierarchy can help control that issue, but the registry record does not report a multiplicity procedure or a testing hierarchy. Consequently, the secondary p-values are best treated as descriptive evidence, not as a collection of definitive tests.

The registry lists additional secondary outcomes involving mean changes in SGRQ, CAT, and BDI/TDI, as well as lung-function measures. Numerical results for the full set of listed secondary outcomes are not reported in the registry record. Conclusions about those measures cannot be drawn from the binary responder summaries alone.

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

• Proportion of Individuals With a 2 Unit Improvement in CAT Without Treatment Failure
• Proportion of Individuals With a 1 Unit Improvement in the BDI/TDI Without Treatment Failure
• Proportion of Individuals With Both a 4 Unit Improvement in SGRQ and a 1 Unit Improvement in BDI/TDI Without Treatment Failure
• Mean Change in St. George's Respiratory Questionnaire (SGRQ)
• Mean Change in COPD Assessment Test (CAT)
• Mean Change in Baseline Dyspnea Index (BDI)/Transition Dyspnea Index (TDI)
• Area Under the Curve (AUC) 0-3 Hours for FEV1
• Change From Baseline in Trough Forced Expiratory Volume Per 1 Second (FEV1) - Absolute Value

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

For a binary outcome, each participant is classified according to whether the event occurred. Here the event is meeting the combined primary endpoint. A risk difference contrasts the proportion with the event in one group against the proportion in the other. A value of zero corresponds to equal observed proportions; a positive or negative value indicates which group had the higher observed proportion according to the subtraction order. The posted unadjusted re-calculation is based on the group counts and denominators, rather than adjustment for other variables.

The primary outcome counts are 128 of 227 for indacaterol/glycopyrrolate and 144 of 244 for placebo. The re-calculated risk difference points toward a lower responder proportion in the active-treatment group. The associated uncertainty interval includes zero, so the posted summary does not establish a clear difference in either direction.

What does the odds ratio add?

The registry’s analysis uses a generalized estimating equation method and reports an odds ratio. Odds compare the chance of the event with the chance of not having the event; an odds ratio contrasts those odds between groups. An odds ratio of 1 corresponds to equal odds. The registry reports an odds ratio of 0.91, with a 95% confidence interval from 0.60 to 1.37. Since this interval includes 1, it includes the no-difference value for the odds ratio. An odds ratio and a risk difference use different scales and should not be read as interchangeable quantities.

General statistical explanation: generalized estimating equations can be used to estimate relationships for outcomes when observations may be correlated, such as repeated measurements or clustered observations. The primary endpoint is described as a participant-level binary outcome, but the registry does not report the specific correlation structure, covariates, or other model details for its GEE analysis. It is therefore not possible to infer those choices from the method label alone.

How should the p-value be read?

A p-value describes how compatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The registry’s analysis reports p = 0.65. The unadjusted re-calculation reports p = 0.564. Both are consistent with the lack of a clear statistical distinction in the posted primary results. The analysis threshold used by the trial sponsor is not reported in the registry record.

General statistical explanation: a p-value is most informative when interpreted alongside the estimated effect, its confidence interval, the outcome definition, and the analysis plan. A result that does not meet a significance threshold is not evidence that two treatments are identical. It can reflect a small effect, imprecise estimation, or both. The registry’s original sample-size justification and assumptions are not reported in the registry record, so the trial’s intended ability to detect a particular difference cannot be assessed from that information.

Why can over-dispersion matter?

General statistical explanation: for count outcomes, over-dispersion occurs when variability is greater than assumed by a basic model. Ignoring it can make uncertainty estimates too small and can lead to overly narrow intervals or misleading tests. The primary outcome is a binary participant count rather than a recurrent-event count, and the registry does not report an over-dispersion assessment for the primary analysis. There is no basis in the registry record to claim that over-dispersion did or did not affect the reported result.

What does recalculation mean?

The posted re-calculation is a simple, unadjusted comparison based on the summary counts and denominators. It does not reproduce the full sponsor analysis, which is reported as a GEE odds-ratio analysis. The two methods address the same broad group comparison but express it on different scales and may use different modeling assumptions. In this trial the discrepancy flag is false, and the overall primary interpretation is consistent: neither posted analysis shows a clear difference between groups. The registry does not report enough model detail to reproduce the sponsor’s analysis independently.

11. Confidence Intervals and Precision

Precision is about how tightly an estimate is determined by the data. A confidence interval gives a range of values compatible with the data and the assumptions of the analysis at the stated confidence level. It does not mean that the true value has a 95% probability of lying within the particular interval after the data have been observed. Rather, the 95% level describes the long-run performance of the interval procedure under its assumptions.

For the sponsor’s primary analysis, the reported odds ratio is 0.91 and its 95% confidence interval runs from 0.60 to 1.37. This interval includes 1, the value corresponding to equal odds. It includes values below 1 and above 1, so the estimate does not precisely distinguish the direction of the underlying odds contrast. The reported p-value is 0.65.

The unadjusted re-calculation is on the risk-difference scale. Its interval includes zero, the value corresponding to equal proportions. This is consistent with the sponsor’s result in the broad sense that neither analysis establishes a clear separation. The interval’s inclusion of zero does not establish exact equality, and its endpoints should be read as reflecting uncertainty rather than as a menu of equally likely treatment effects.

The primary endpoint denominators were 227 and 244. Even with hundreds of participants in the outcome groups, the estimate is not sufficiently precise in the posted analysis to rule out differences in either direction. Precision should be considered together with the endpoint’s clinical definition, the original design assumptions, and the analysis plan. The original sample-size justification and those design assumptions 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 illustrations translate the observed effect into hypothetical sample-size requirements under stated assumptions; they do not describe the trial’s actual enrollment plan. For these binary outcomes, the figures are participants per arm, not a total across both arms and not a total number of events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. The original trial design assumptions are not reported in the registry record.

The 80% power column gives the hypothetical number of participants per arm for an 80% chance of detecting the specified effect under those assumptions, if that effect is the true one and the model assumptions hold. The 90% power column uses the same interpretation with a higher target chance of detection. These are planning targets, not guarantees about an individual study.

The rows use 100%, 75%, and 50% of the observed effect. As the target effect gets smaller, the required number of participants increases. For the primary outcome, planning for 100% of the observed effect gives 5,544 participants per arm for 80% power and 7,421 for 90% power. Planning for 75% gives 9,835 and 13,166, respectively; planning for 50% gives 22,081 and 29,560. These illustrations can be very large when the observed difference is small, and should not be read as an endorsement of the observed effect as the true effect. This is not observed power.

The planning values are sensitive to the observed effect used as their starting point. They are therefore illustrations of how assumptions affect a future design, not evidence about the probability that the completed trial was successful. Any curve associated with these calculations should be interpreted in the same planning context: smaller effects require larger samples under the stated assumptions.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.590; treatment proportion p₁ = 0.564; average p̄ = 0.577.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6987 = 1.3694.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6984 = 0.5878.
4. n = (1.3694 + 0.5878)² / (-0.0263)² = 5,543.3, rounded up to 5,544 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
p0 <- 0.590163934426229                          # control proportion
p1 <- 0.563876651982379                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(2867761)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 5,544 (80% power), 7,421 (90% power)
 75% of observed effect: n per arm = 9,835 (80% power), 13,166 (90% power)
 50% of observed effect: n per arm = 22,081 (80% power), 29,560 (90% power)
power.prop.test: 5543.3 
Simulated power at n = 5,544 per arm: 0.796 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry’s own primary analysis is a generalized estimating equation analysis reporting an odds ratio of 0.91, a 95% confidence interval from 0.60 to 1.37, and p = 0.65. The unadjusted re-calculation instead uses the primary outcome counts to express a risk difference and reports p = 0.564. These are different statistical methods and effect scales; the re-calculation is not a replacement for the sponsor’s analysis.

The sponsor’s result is the analysis to prioritize when describing the trial’s reported inferential result. The discrepancy flag is false, and both analyses point to the same broad reading: the posted results do not show a clear difference in the primary responder outcome. The sponsor’s interval includes the no-difference value for an odds ratio, while the unadjusted risk-difference interval includes zero.

The registry does not report enough detail to reconstruct the sponsor’s GEE model, including any covariate adjustment or correlation structure. Nor does it report the full prespecified analysis plan. The simple re-calculation is useful as a transparent comparison based on posted summary counts, but it cannot recover information about individual participants or reproduce adjustments that may have been used in the sponsor’s analysis.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity, missing-data handling, and analysis populations affect how confidently the posted results can be interpreted. The registry lists 14 outcome measures and 12 analyses. Looking at several outcomes creates multiple opportunities for apparently notable results to arise by chance. A prespecified testing hierarchy or statistical adjustment can address this concern, but whether either was used is not reported in the registry record. The registry also does not report the trial’s full statistical analysis plan or how the primary outcome’s place in any testing sequence was determined.

The primary outcome description contains information about exclusions and missing SGRQ assessments. In the indacaterol/glycopyrrolate arm, it states that 5 subjects had a primary efficacy assessment at least 4 weeks after the last visit and were not included in the mITT, followed by 1 additional subject missing SGRQ at the final visit. It also begins to describe similar exclusions in the placebo arm, but the recorded description is incomplete. The full analysis-population rules and the handling of missing outcome data are not reported in the registry record.

The displayed primary denominators are 227 and 244, while the safety summaries use at-risk counts of 261 and 274. These figures describe different analysis summaries and should not be assumed to represent the same population. The registry record does not provide a complete participant flow or enough information to explain every difference between enrollment and the outcome-specific denominators.

General statistical explanation: excluding participants with missing outcomes can affect a comparison if missingness is related to treatment assignment, outcome status, or both. Different missing-data assumptions can lead to different estimates. Without the analysis-population definitions, missingness patterns, and imputation or sensitivity-analysis details, it is not possible to determine how robust the primary estimate is to missing data. These limitations do not establish that the result is biased; they identify information needed to evaluate that possibility.

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

Serious events with the highest arm-level rate: motor vehicle accident (0.4%), abdominal pain (0.4%), anastomotic ulcer (0.4%), breakthrough seizures (0.4%), gastric gj junction ulcer and posterior wall perforation (0.4%).

The safety summary lists serious adverse events in 4 of 261 participants at risk in the indacaterol/glycopyrrolate group and 8 of 274 at risk in the placebo group. The registry records 0 deaths in each group and 0 other adverse events in each group. These counts are descriptive safety data; they are not the primary efficacy comparison and should not be interpreted as a complete assessment of all possible harms.

The registry lists serious-event terms including Motor Vehicle Accident, Abdominal Pain, Anastomotic Ulcer, Breakthrough Seizures, Gastric GJ junction ulcer and posterior wall perforation, and Postprocedural Intraabdominal Abscess. Each listed term is accompanied by 0.4%. These event terms do not, by themselves, indicate that the study treatment caused an event. The registry record does not report attribution, event-level timing, or further details for interpreting these terms.

The at-risk safety counts differ from the primary outcome denominators. Safety counts and efficacy counts answer different questions and can use different analysis populations. A comparison of serious-event counts alone does not establish whether groups have equivalent safety profiles, particularly without additional detail about event definitions, follow-up, and attribution.

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

The primary results describe the proportion of analyzed participants who achieved a specified SGRQ improvement without meeting the registry’s treatment-failure definition. The observed counts were 128 of 227 in the indacaterol/glycopyrrolate group and 144 of 244 in the placebo group. The unadjusted comparison and the sponsor’s GEE analysis both leave substantial uncertainty about the underlying group difference. The sponsor’s reported odds-ratio interval includes 1, and the re-calculated risk-difference interval includes zero.

This does not mean the treatments have been shown to be identical. A result without a clear statistical difference is not a formal demonstration of equivalence or non-inferiority. Such conclusions require appropriate design objectives, margins, and analyses; these are not reported in the registry record. Nor do the posted data establish that every participant experienced the same symptom change, since the endpoint reduces SGRQ changes to a responder category and combines that response with treatment-failure status.

The findings are limited to the registered population, comparison, regimen, and 12-week treatment period. They do not establish what would happen with different doses, treatment durations, patient groups, or longer-term follow-up. The registry hypothesis concerns symptomatic current and former smokers with spirometric values in the normal range; generalization beyond that group requires evidence not contained in these results.

The secondary outcomes provide additional descriptive information, but the posted binary comparisons do not create a consistent basis for a broader conclusion. The registry’s missing details about multiplicity, missing-data handling, and the original analysis plan also limit a full audit of the results. Overall, the posted primary data show no clear difference in the defined responder outcome, while leaving uncertainty about the range of possible underlying differences.

18. Why This Trial Matters Statistically

This trial raises a statistical question about how to evaluate a treatment in a population selected for symptoms despite spirometric values described as normal. Its primary endpoint is not simply a mean questionnaire change: it asks whether participants achieved a minimum clinically important SGRQ improvement and avoided a specified treatment failure. That combined definition makes the estimand understandable in patient-centered terms, while also making clear that the outcome reflects more than one component.

The analysis illustrates why effect estimates and uncertainty intervals are more informative than a binary focus on whether a p-value crosses a threshold. The primary group counts are fairly close, and both the sponsor analysis and the unadjusted re-calculation are compatible with no clear difference. At the same time, absence of a clear difference is not the same as proof of no effect. Precision and design assumptions matter to that distinction.

RETHINC also illustrates how different analysis scales can describe the same broad comparison. The registry reports an odds ratio from a GEE analysis, while the posted simple re-calculation uses a risk difference. Each has a different interpretation, and neither should be substituted for the other without stating the scale and method. The registry’s limited reporting of the analysis plan and population details makes it important to distinguish the sponsor’s reported analysis from a summary-count re-calculation.

Finally, the multiple listed outcome measures and incomplete details about multiplicity and missing data show why registry results need to be read alongside analysis specifications. The posted findings are useful for understanding the measured outcomes, but a full statistical audit requires information not reported in the registry record.

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.

Several trial-specific details needed for a complete statistical appraisal are not reported in the registry record. These include the original sample-size justification, the prespecified analysis plan, interim analyses, allocation-concealment procedures, and the specific roles covered by quadruple masking. The registry also does not give enough detail to reconstruct the sponsor’s GEE model or to determine whether covariates or a particular correlation structure were used.

The primary outcome description gives partial information about exclusions and a missing final-visit SGRQ assessment, but the placebo-arm description is incomplete. Full participant-flow information, complete analysis-population definitions, missing-data handling, and sensitivity analyses are not reported in the registry record. This leaves uncertainty about how the posted denominators relate to all randomized participants and how missing outcome information was addressed.

The registry lists many outcomes, but does not report a multiplicity procedure or testing hierarchy. That limits how strongly secondary p-values can be interpreted. Numerical results for the full set of listed secondary outcomes are not reported in the registry record, so the secondary binary comparisons cannot stand in for the full set of planned measurements.

The primary endpoint is a combined responder outcome at 12 weeks. It conveys whether participants met a threshold and avoided treatment failure, but it does not preserve the full distribution of SGRQ changes or show the longer-term course of symptoms. The safety summary provides serious-event counts and selected terms but does not include attribution or detailed event narratives. These limits constrain interpretation; they do not, by themselves, establish that the results are invalid.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: RETHINC: REdefining THerapy In Early COPD for the Pulmonary Trials Cooperative — NCT02867761.
• Registry record last updated 2023-04-13; status last verified 2023-04.
• Results first posted 2022-08-30.
• 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

RETHINC is a completed phase 3 randomized, quadruple-masked, parallel-group trial sponsored by the University of Michigan. The registry reports enrollment of 780 and compares indacaterol/glycopyrrolate 27.5/15.6 mcg inhaled twice daily with placebo for 12 weeks in symptomatic current and former smokers with spirometric values in the normal range.

The primary endpoint was a 4-unit SGRQ improvement at 12 weeks without treatment failure. The posted counts were 128 of 227 for indacaterol/glycopyrrolate and 144 of 244 for placebo. The sponsor reports an odds ratio of 0.91, a 95% confidence interval from 0.60 to 1.37, and p = 0.65. The unadjusted re-calculation also does not show a clear difference.

Secondary binary outcomes show a mixed pattern, and serious adverse events were recorded in both groups. Important details about the original design assumptions, multiplicity, missing-data handling, and full analysis plan are not reported in the registry record.