Efficacy, Pharmacokinetics (PK), Safety and Tolerability Study of Inhaled AZD8871: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy, Pharmacokinetics (PK), Safety and Tolerability Study of Inhaled AZD8871 (NCT02971293), a randomized phase 2 study. The primary outcome is Change From Baseline in Trough Forced Expiratory Volume in 1 Second (FEV1).

2. Clinical Question

The trial also compared the two AZD8871 doses in a sponsor-reported analysis. Its crossover design means participants received three treatments in a random order, rather than being assigned to only one treatment throughout the study. The registry lists 42 enrolled participants, while the primary endpoint summaries report treatment-specific analysis counts of 34 for AZD8871 100 µg, 39 for AZD8871 600 µg, and 36 for placebo. These treatment-specific counts should not be added to infer the number of individual participants, because the design is crossover.

3. Trial Design

This was a Phase IIa, randomised, multicentre, double-blind, placebo-controlled, three-period crossover study of inhaled AZD8871 in people with moderate to severe COPD. Each participant was intended to receive AZD8871 100 µg, AZD8871 600 µg, and placebo once daily for 2 weeks per treatment, in a random order. The registry summary describes blinding of both patients and the study doctor.

The crossover structure allows treatment comparisons to be made within a participant as well as across treatment periods. In general, within-participant comparisons can reduce the influence of stable differences between individuals. They also require suitable handling of period, sequence, and possible carryover effects. The exact model terms used in the sponsor’s analysis, and how these design features were handled, are not reported in the registry record. The sponsor’s analyses are identified as ANCOVA, but the record does not provide further model detail.

The registry reports 42 enrolled participants and identifies the primary endpoint population as the full analysis set: all randomised patients who received at least one dose of investigational product, irrespective of protocol adherence and continued participation. Treatment-specific primary endpoint summaries include 34, 39, and 36 participants for the respective treatments. These are analysis counts by treatment and do not establish a count of unique individuals.

The registry summary describes 12 visits for each patient over a period of 4 to 6 months. The study status is completed. The dates recorded for study start and primary completion are 2016-12-15 and 2017-08-18. The detailed sequence allocation, washout arrangements, and original design assumptions are not reported in the registry record.

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: A total of 103 patients were screened; 42 patients were eligible to participate and were randomised.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS): all randomised patients who received at least one dose of the IP, irrespective of their protocol adherence and continued participation in the study.

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: Safety analysis set: Includes all randomised participants who received at least one dose of investigational product.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Trough Forced Expiratory Volume in 1 Second (FEV1), measured over On Day 15.

The primary endpoint was change from baseline in trough FEV1 on Day 15, measured in litres. FEV1 is the amount of air a person can forcefully exhale in the first second of a breathing test. “Trough” refers to the measurement taken before a scheduled dose, as described by the endpoint title and timing. The registry describes the endpoint as an assessment of the efficacy of inhaled AZD8871 in patients with moderate to severe COPD.

Change from baseline expresses the follow-up measurement relative to the participant’s starting measurement. In general, this can help focus the comparison on change during treatment rather than on differences in starting lung function. The posted treatment summaries are least-squares means with standard errors, not raw individual observations. A least-squares mean is a model-based average; the exact adjustment terms used to obtain these means are not reported in the registry record.

FEV1 is used as a quantitative measure of airflow because it records a volume rather than a categorical judgement. A continuous outcome can retain information about the magnitude of measured change, while its interpretation still depends on the measurement context, uncertainty, and analysis model. The registry record does not give a threshold for a clinically important change, so the posted estimates alone do not establish whether a difference is clinically meaningful.

The endpoint was assessed on Day 15 after the 2-week treatment period. The registry also lists other FEV1 measurements at earlier times and across the treatment duration, but these are secondary outcomes and do not replace the prespecified primary endpoint.

7. Results Posted in the Registry

• AZD8871 100 µg: mean 0.17 versus 0.01 on control; difference 0.16 (95% CI 0.06 to 0.26), standardized effect d = 0.75; z-test p = 0.002.
• AZD8871 600 µg: mean 0.27 versus 0.01 on control; difference 0.26 (95% CI 0.16 to 0.36), standardized effect d = 1.20; 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.

Change From Baseline in Trough FEV1 at Day 1 (Single 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:
  • AZD8871 100 µg: mean 0.09 versus 0.01 on control; difference 0.09 (95% CI 0.01 to 0.17), standardized effect d = 0.51; z-test p = 0.033.
  • AZD8871 600 µg: mean 0.16 versus 0.01 on control; difference 0.15 (95% CI 0.08 to 0.23), standardized effect d = 0.92; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for AZD8871 100 µg 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 AZD8871 600 µg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Trough FEV1 at Day 8 (Pre-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:
  • AZD8871 100 µg: mean 0.18 versus 0.03 on control; difference 0.15 (95% CI 0.06 to 0.24), standardized effect d = 0.78; z-test p = 0.001.
  • AZD8871 600 µg: mean 0.23 versus 0.03 on control; difference 0.20 (95% CI 0.12 to 0.28), standardized effect d = 1.07; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for AZD8871 100 µg 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 AZD8871 600 µg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Trough FEV1 Over the Treatment Duration (Days 1-15)

• 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:
  • AZD8871 100 µg: mean 0.15 versus 0.02 on control; difference 0.13 (95% CI 0.05 to 0.21), standardized effect d = 0.79; z-test p = 0.001.
  • AZD8871 600 µg: mean 0.21 versus 0.02 on control; difference 0.20 (95% CI 0.12 to 0.27), standardized effect d = 1.20; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for AZD8871 100 µg 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 AZD8871 600 µg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary FEV1 summaries follow the same broad direction as the primary endpoint: the treatment means for both AZD8871 doses exceed the placebo mean at Day 1, at Day 8 before dosing, and over Days 1-15. The registry also reports sponsor ANCOVA superiority analyses for both active doses versus placebo at these listed secondary FEV1 assessments. These additional measurements provide context for the primary Day 15 result, but they are not independent replications because they come from the same trial and participant population.

The registry lists pharmacokinetic outcomes for AZD8871 and its metabolites, including maximum plasma concentration, time to maximum concentration, and area-under-the-curve measures after single and multiple doses. Numerical results for those listed pharmacokinetic measures are not reported in the registry record. The record identifies 26 secondary outcomes as posted, but the available detail does not support a complete interpretation of each outcome.

In general, secondary outcomes can help describe consistency across measures and time points, but they carry less inferential weight when many outcomes or comparisons are considered and the multiplicity approach is not documented. The registry record does not report whether the sponsor adjusted secondary analyses for multiple testing, nor does it provide a complete statistical plan. A nominally small p-value among secondary outcomes should therefore not be treated as equivalent to a primary endpoint result with a fully documented analysis plan. The secondary findings are best read as supportive context, with their precision and multiplicity limitations kept in view.

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

• Observed Maximum Plasma (Cmax) of AZD8871 and Its Metabolites (Single Dose)
• Observed Maximum Plasma (Cmax) of AZD8871 and Its Metabolites (Multiple Doses, Day 14)
• Time to Reach Maximum Plasma Concentration (Tmax) of AZD8871 and Its Metabolites (Single Dose)
• Time to Reach Maximum Plasma Concentration (Tmax) of AZD8871 and Its Metabolites (Multiple Doses, Day 14)
• AUClast of AZD8871 and Its Metabolites (Single Dose)
• AUClast of AZD8871 and Its Metabolites (Multiple Doses, Day 14)
• AUC0-24 of AZD8871 and Its Metabolites (Single Dose)
• AUC0-24 of AZD8871 and Its Metabolites (Multiple Doses, Day 14)

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary estimate represent?

The primary outcome is continuous: change in trough FEV1 from baseline, expressed in litres. The registry reports least-squares means and standard errors for each treatment. In general, a least-squares mean is an estimate from a statistical model, rather than simply the arithmetic mean of all observed measurements. It can account for terms included in that model. The registry identifies the sponsor’s comparison method as ANCOVA, but the adjustment variables and model details are not reported in the registry record.

A standard error describes uncertainty in an estimated mean under its statistical model. It is not the same as the spread of individual participant measurements. Smaller standard errors generally indicate more precise estimates, but interpretation also depends on the model and the amount of information in the data. The record gives standard errors for the treatment means, but does not report the participant-level data needed to independently verify the fitted model.

How should the sponsor’s ANCOVA be understood?

ANCOVA is analysis of covariance. In general, it compares outcome means while adjusting for one or more covariates. It can account for baseline measurements or other prespecified factors when those are included in the model. In this study, the sponsor identifies ANCOVA as the method for its superiority comparisons. The registry does not report the covariates, the handling of treatment period and sequence, or the exact model specification. Those omissions matter in a crossover trial because measurements from the same participant are related, and treatment sequence and period can be relevant to the comparison.

The sponsor reports p-values for comparisons of each active dose with placebo and for a comparison between the active doses. The record does not give the sponsor’s corresponding contrast estimates or confidence limits. A p-value alone does not communicate the size of a difference, and it cannot substitute for an estimate with an uncertainty interval.

What are the recalculated comparisons?

The recalculated comparisons use the posted treatment means and standard errors to form simple unadjusted comparisons. For Day 15, the recalculated mean differences versus placebo are 0.161 L for AZD8871 100 µg and 0.26 L for AZD8871 600 µg. The associated recalculated p-values are 0.002 and <0.001. These are not adjusted crossover-model estimates. The recalculation uses approximate variability derived from the posted summary statistics, rather than participant-level observations or the sponsor’s ANCOVA output.

In general, an unadjusted comparison may omit features accounted for by a trial’s planned model. A crossover comparison also needs to reflect the fact that a participant may contribute measurements under more than one treatment. Treating treatment summaries as if they were independent groups can therefore fail to represent the study design. The recalculated values provide a transparent, simple comparison of the posted summaries, but should not be taken as a reconstruction of the sponsor’s analysis.

What does a confidence interval communicate?

In general, a confidence interval describes the range of estimates compatible with the data and the method used, at a stated confidence level. Wider intervals indicate less precision, while narrower intervals indicate greater precision, conditional on the assumptions of the analysis. The recalculated comparison intervals for the primary endpoint are given with the posted summary statistics, but the confidence level is not reported in the registry record. The sponsor’s ANCOVA comparisons do not include reported confidence limits or effect estimates in the registry entry.

The interval limits for the recalculated comparisons are not a substitute for the sponsor’s adjusted results. They are based on a different, unadjusted method and should be interpreted alongside the stated discrepancy. The sponsor’s own analysis takes precedence when describing the trial’s primary inferential result.

Why does the crossover design matter?

In general, a crossover design uses participants as their own comparison across treatment periods. This can reduce the effect of stable between-person differences, but the analysis must account for the repeated measurements and treatment sequence. It also relies on design and analysis assumptions about changes over time and any residual influence of previous treatment. The registry describes three treatment periods and random treatment order, but the washout details and the sponsor’s treatment of period, sequence, or carryover are not reported in the registry record.

The treatment-specific analysis counts are 34, 39, and 36. They are not independent parallel-group sample sizes, and they should not be summed as a count of individual participants. The registry does not provide a participant flow by treatment period or explain the differing analysis counts.

How should the p-values be read?

In general, a p-value is calculated under a null hypothesis and the assumptions of an analysis. A small p-value indicates that data at least as incompatible with that null as the observed data would be unusual under those assumptions. It does not quantify the probability that the null is true, establish clinical importance, or measure the size of an effect. The sponsor’s reported p-values and the recalculated unadjusted p-values answer related but not identical statistical questions because they come from different analyses.

The registry record does not report whether or how the sponsor adjusted for multiple comparisons. That omission is relevant because several treatment comparisons and outcomes are listed. No unreported adjustment should be assumed. The reported significance labels therefore need to be read in the context of the available analysis detail and the absence of a documented multiplicity strategy.

11. Confidence Intervals and Precision

The primary treatment means are reported with standard errors: 0.168 L (0.037) for AZD8871 100 µg, 0.267 L (0.035) for AZD8871 600 µg, and 0.007 L (0.036) for placebo. In general, standard errors describe the precision of estimated means, while confidence intervals express uncertainty around an estimate over a range of values under a specified method. The standard errors do not describe the range of individual FEV1 changes.

The simple recalculated mean difference for AZD8871 100 µg versus placebo is 0.161 L, with an interval from 0.060 to 0.262. For AZD8871 600 µg versus placebo, the recalculated mean difference is 0.26 L, with an interval from 0.162 to 0.358. These intervals are from the unadjusted recalculations, not the sponsor’s ANCOVA model. The confidence level for these intervals is not reported in the registry record, and the sponsor’s own contrast intervals are also not reported there.

In general, an interval’s width reflects both the observed data and the assumptions of the method. A narrower interval indicates greater statistical precision under those assumptions, but precision is not the same as clinical importance or freedom from bias. In this case, the interval estimates depend on approximate variability derived from summary data and do not model the crossover structure as the sponsor’s analysis may have done. The discrepancy flag reinforces that they should not displace the sponsor’s analysis.

The registry does not provide the full ANCOVA estimates, covariance structure, or participant-level data needed to evaluate the sponsor’s precision estimates independently. The reported p-values alone cannot show how narrowly or broadly the sponsor’s adjusted effects are estimated.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures describe participants per arm for the listed power targets; they are not total event counts. The planning illustration assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It uses the observed effect as its reference and considers detecting the stated fraction of that observed effect. These are planning assumptions for the illustration, not the original trial’s design assumptions, which are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design intended to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect and those assumptions were correct. The 90% power column describes the corresponding planning target for a 90% chance. These figures are not evidence that the completed study had that probability of detecting its result; this is not observed power.

The rows for 100%, 75%, and 50% of the observed effect show how the illustrative sample requirement changes when the target effect is smaller. For example, for the AZD8871 100 µg versus placebo comparison, planning for 75% of the observed effect gives 51 participants per arm for 80% power and 68 participants per arm for 90% power. For the AZD8871 600 µg versus placebo comparison, those figures are 20 and 27 participants per arm. Planning for 50% of the observed effect requires more participants per arm than planning for the full observed effect. In general, smaller effects need more participants to detect under otherwise unchanged assumptions.

These calculations use a two-arm, equal-allocation illustration. They do not reproduce the crossover design or establish what the original study was designed to detect. The original sample-size justification and its assumptions 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 = 0.161; pooled standard deviation σ = 0.216.
2. n = 2 × (1.96 + 0.842)² × 0.216² / 0.161² = 28.2, rounded up to 29 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.161                      # observed difference in means
sigma <- 0.215876394372008                     # 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(2971293)
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 = 29 (80% power), 38 (90% power)
 75% of observed effect: n per arm = 51 (80% power), 68 (90% power)
 50% of observed effect: n per arm = 113 (80% power), 152 (90% power)
power.t.test: 29.2 
Simulated power at n = 29 per arm: 0.794 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s registry-reported analysis uses ANCOVA and identifies superiority comparisons. For the primary Day 15 outcome, the sponsor reports p < 0.001 for AZD8871 100 µg versus placebo, p < 0.001 for AZD8871 600 µg versus placebo, and p = 0.020 for the comparison between active doses. The registry does not report the sponsor’s effect estimates or confidence limits for these comparisons.

The recalculated comparisons use only the posted treatment means and standard errors and are simple, unadjusted estimates. They give a mean difference of 0.161 L for AZD8871 100 µg versus placebo, with p = 0.002, and 0.26 L for AZD8871 600 µg versus placebo, with p < 0.001. They are not a reproduction of the sponsor’s ANCOVA and do not account for the crossover structure using participant-level data.

A discrepancy is flagged between the recalculated results and the sponsor analysis. Accordingly, the sponsor’s own analysis takes precedence for the trial’s inferential finding. The recalculations can serve as a transparent descriptive check on the posted summary values, but they should not be substituted for the sponsor’s model-based comparisons or used to infer the unreported details of that model.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint, multiple secondary outcomes, and several treatment comparisons. In general, testing many hypotheses increases the chance that at least one result will appear statistically notable by chance if each test is considered separately. A multiplicity strategy may control that risk by adjusting significance thresholds or by specifying a hierarchy for testing. The registry record does not report a multiplicity adjustment, a hierarchy among secondary outcomes, or a complete statistical analysis plan. No particular strategy should be assumed.

The sponsor reports ANCOVA p-values for the primary treatment comparisons and for several secondary FEV1 comparisons. The registry does not provide the model details, adjusted effect estimates, or confidence limits for these sponsor analyses. This limits independent assessment of both the multiplicity approach and the statistical uncertainty around the sponsor’s contrasts.

The primary population is defined as the full analysis set: all randomised patients who received at least one dose of investigational product, irrespective of protocol adherence or continued study participation. The record gives treatment-specific counts for the outcome summaries, but does not report a participant flow, reasons for missing endpoint measurements, or how missing observations were handled in the sponsor’s model. The missing-data assumptions and sensitivity analyses are not reported in the registry record.

In general, missing measurements can affect estimates if the participants or treatment periods without observed outcomes differ systematically from those with observed outcomes. The registry record does not provide enough detail to judge that possibility or to determine whether the sponsor used imputation or another missing-data method. It also does not report interim analyses or stopping rules. These omissions do not establish that such procedures were or were not used; they mean they are not reported in the registry record.

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: abdominal wall abscess (2.8%), appendicitis (2.8%), chronic obstructive pulmonary disease exacerbation (2.6%).

The registry records serious adverse events affecting 0 participants in the AZD8871 100 µg group, 1 in the AZD8871 600 µg group, and 1 in the placebo group. The corresponding numbers at risk are 34, 39, and 36. Deaths are recorded as 0 in each treatment group. The registry also reports other adverse events affecting 5, 7, and 5 participants, respectively, with the same treatment-specific numbers at risk as the serious-event summaries.

These figures describe the posted counts; they do not establish that the treatments have equivalent safety profiles. In a crossover study, treatment-specific exposure and event attribution require careful interpretation, and the registry does not provide event timing, duration, severity detail, or a full account of how events were assigned to treatment. Serious-event terms listed in the record include abdominal wall abscess, appendicitis, and chronic obstructive pulmonary disease exacerbation, with percentages of 2.8%, 2.8%, and 2.6%, respectively. The registry record does not provide enough detail to interpret those term percentages beyond their listing.

Safety comparisons from a trial of this size and duration may be imprecise for uncommon events. The posted counts are descriptive and should be read alongside the limited duration and the absence of detailed event-level information in the registry record.

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

The posted primary results describe mean changes in trough FEV1 on Day 15 during the study’s treatment periods. Both active-treatment means are higher than the placebo mean, and the sponsor reports superiority p-values for both active doses versus placebo. The sponsor also reports a statistically significant comparison between active doses. The registry does not provide the sponsor’s contrast estimates or confidence limits, so the magnitude and precision of those adjusted comparisons cannot be fully assessed from the sponsor’s reported results.

The simple recalculations quantify unadjusted mean differences from the posted summary statistics, but they are not equivalent to the sponsor’s ANCOVA analysis. Because the registry flags a discrepancy, the sponsor’s own analysis takes precedence. The recalculated results should be read as a separate, approximate summary, not as a replacement for the trial’s reported model.

In general, statistical evidence of a difference does not by itself establish that the difference is important to patients. The registry record does not report a threshold for clinically meaningful FEV1 change, nor does it provide patient-reported outcomes that would establish how the measured changes related to symptoms or daily functioning. The result also does not determine whether any effect persists beyond the measured treatment period.

The findings apply to the trial population and conditions described in the registry, not automatically to other populations, treatment durations, or clinical settings. The study was a Phase IIa crossover trial with a short treatment period. It does not establish long-term outcomes or resolve the full safety profile. The record’s missing details about the statistical model, multiplicity, and missing-data handling also limit independent appraisal. The results should therefore be understood as the reported findings of this specific study rather than a general conclusion about treatment for COPD.

18. Why This Trial Matters Statistically

This study is statistically informative because it used a randomised, double-blind, placebo-controlled crossover design to compare two doses with placebo. In general, a crossover design can make within-participant comparisons possible, which may reduce the influence of stable differences between participants. At the same time, it requires analysis that respects repeated observations and treatment periods. The registry identifies the sponsor method as ANCOVA but does not report enough model detail to evaluate how the crossover structure was handled.

The record makes an important distinction between sponsor-reported inference and simple recalculation. The sponsor’s p-values come from ANCOVA, while the recalculated comparisons use posted treatment means and standard errors. Those approaches are not interchangeable. The discrepancy flag makes it especially important to keep the sponsor analysis as the primary inferential result and to treat the recalculation as an approximate, unadjusted check.

The study also illustrates why estimates and uncertainty matter alongside p-values. The treatment means and standard errors convey some information about the outcome summaries, while the registry does not report adjusted sponsor contrasts or their confidence limits. Without those, the statistical significance labels do not show the precision or size of the sponsor’s model-based effects directly.

Finally, multiple outcomes and comparisons are present, but multiplicity handling is not reported. Reading the secondary findings as contextual rather than definitive avoids giving each nominal test the same weight as the primary comparison. The registry’s incomplete reporting of model details, missing-data methods, and original sample-size assumptions also shows how those details affect interpretation of even a completed trial.

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 limitations are specific to interpreting this trial’s registry results. The design is crossover, but the registry does not report the washout arrangement, treatment-period and sequence terms, or how possible carryover was handled in the analysis. The sponsor identifies ANCOVA but does not provide the complete model specification, adjusted contrasts, or contrast confidence limits.

The posted treatment summaries include different analysis counts for the three treatments. The registry defines the full analysis set but does not provide participant flow by period, reasons for missing observations, or the method used to handle missing data. Because treatment-specific observations in a crossover trial may come from the same participants, the counts cannot be treated as independent parallel groups or added to infer a unique-participant total.

The recalculated differences are approximate and unadjusted, based on summary statistics rather than individual data. A discrepancy is flagged, so the sponsor’s own analysis takes precedence. The registry also does not report the confidence level for the recalculated intervals, and the sponsor’s adjusted effect intervals are not available in the record.

Multiplicity handling is not reported despite the several outcomes and comparisons. The original sample-size justification, interim-analysis plan, and detailed statistical analysis plan are also not reported in the registry record. The primary outcome is a lung-function measure, but the registry does not give a clinically important threshold for interpreting the size of change. Finally, the study describes treatment over 2 weeks and does not establish longer-term outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy, Pharmacokinetics (PK), Safety and Tolerability Study of Inhaled AZD8871 — NCT02971293.
• Registry record last updated 2019-06-18; status last verified 2019-06.
• Results first posted 2019-06-18.
• 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

NCT02971293 is a completed Phase IIa randomised, double-blind, placebo-controlled, three-period crossover study of inhaled AZD8871 in patients with moderate to severe COPD. Participants received AZD8871 100 µg, AZD8871 600 µg, and placebo once daily for 2 weeks in random order. The primary endpoint was change from baseline in trough FEV1 on Day 15.

The posted primary least-squares mean changes were 0.168 L for AZD8871 100 µg, 0.267 L for AZD8871 600 µg, and 0.007 L for placebo. The sponsor reports ANCOVA superiority p-values of <0.001 for each active dose versus placebo and 0.020 for the comparison between doses. Simple unadjusted recalculations are also available, but a discrepancy is flagged and the sponsor’s analysis takes precedence.

The record does not report the full sponsor model, adjusted effect estimates, multiplicity strategy, or missing-data methods. Secondary FEV1 summaries follow the same broad direction, while numerical results for the listed pharmacokinetic outcomes are not reported in the registry record.