A Phase II Study to Evaluate the Efficacy, Safety and Tolerability of AZD5069 in Patients With Uncontrolled Persistent Asthma.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase II Study to Evaluate the Efficacy, Safety and Tolerability of AZD5069 in Patients With Uncontrolled Persistent Asthma. (NCT01704495), a randomized phase 2 study. The primary outcome is Rate of Severe Asthma Exacerbations During 6 Months.

2. Clinical Question

3. Trial Design

The registry describes a Phase II, randomized, double-blind, placebo-controlled, multi-centre, parallel-group study of AZD5069 in patients with uncontrolled persistent asthma. It also labels masking as triple; which parties were masked is not reported in the registry record. The study evaluated AZD5069 at 5 mg, 15 mg, and 45 mg, taken twice daily as oral capsules, against placebo capsules taken twice daily. Treatment was intended as an addition to medium to high dose inhaled corticosteroids and long-acting β2 agonists.

The registry lists enrollment as 1147 and the study status as completed. The recorded start is 2012-11 and primary completion is 2014-08. The official title describes a 6-month treatment period and an optional safety extension of up to 6 months. The number of participants in each arm of the primary outcome analysis differs from the overall enrollment; reasons for these analysis-set counts are not reported in the registry record.

The primary outcome was the rate of severe asthma exacerbations during treatment up to 6 months, analyzed in the full analysis set. The record lists 42 outcome measures and 41 posted secondary outcomes. These include asthma-related hospital or intensive care admissions, measures of lung function, asthma control and quality of life, and oral corticosteroid use. The registry record does not report the original sample-size justification, the detailed statistical analysis plan, or how participants were assigned to the full analysis set. It also does not report whether or how the optional safety extension affected outcome analyses.

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: 4 weeks run-in period on background therapy prior to randomization. The discrepancy in the number of enrolled patients compared to the protocol section (n=1147) is because of a patient was in error reported by a monitor as enrolled when the patient was in effect not enrolled.

Subjects Randomized

Reasons for not completing this period:

Optional Safety Extension

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full 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 Rate of Severe Asthma Exacerbations During 6 Months, measured over From start of treatment up to 6 months.

The primary endpoint is the rate of severe asthma exacerbations during treatment from the start of treatment up to 6 months. The outcome is expressed as exacerbations per 6 month, and the registry describes the arm-level estimates as least-squares means with 90% confidence intervals. The analysis population is identified as the full analysis set.

A rate represents events in relation to a period of observation, so it can describe recurrent events rather than only whether a participant had any event. This can be useful when the clinical question concerns the frequency of exacerbations over a treatment period. A rate comparison is not the same as comparing the proportion of participants with an exacerbation: participants may contribute different numbers of events, and the approach depends on how exposure time and event counts are handled. The detailed sponsor model specification and handling of exposure are not reported in the registry record.

In the posted arm-level estimates, the AZD5069 rates are 0.31 for 45 mg, 0.31 for 15 mg, and 0.26 for 5 mg; the placebo rate is 0.2. The respective 90% confidence intervals are 0.2 to 0.5, 0.19 to 0.49, 0.16 to 0.42, and 0.12 to 0.33. These estimates describe the reported endpoint and its uncertainty. They do not, by themselves, establish a treatment effect; the registry also reports sponsor comparisons that differ from simple unadjusted recalculations.

7. Results Posted in the Registry

• AZD5069 45 mg BID: 0.31 versus 0.20 (Exacerbations per 6 month) on control; rate ratio 1.55 (95% CI 1.29–1.86, approximate, Poisson model); p ≈ <0.001.
• AZD5069 15 mg BID: 0.31 versus 0.20 (Exacerbations per 6 month) on control; rate ratio 1.55 (95% CI 1.29–1.86, approximate, Poisson model); p ≈ <0.001.
• AZD5069 5 mg BID: 0.26 versus 0.20 (Exacerbations per 6 month) on control; rate ratio 1.30 (95% CI 1.08–1.57, approximate, Poisson model); p ≈ 0.007.

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.

Rate of Asthma-specific Hospital Admission/Intensive Care Unit Admissions During 6 Months

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • AZD5069 45 mg BID: 0.04 versus 0.02 (Exacerbations per 6 month) on control; rate ratio 2.00 (95% CI 1.16–3.46, approximate, Poisson model); p ≈ 0.013.
  • AZD5069 15 mg BID: 0.02 versus 0.02 (Exacerbations per 6 month) on control; rate ratio 1.00 (95% CI 0.53–1.90, approximate, Poisson model); p ≈ 1.000.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically higher for AZD5069 45 mg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between AZD5069 15 mg BID and the control. The interval gives the range of effects that remain compatible with the data.

Number of Patients Presenting Improvement From Baseline to End of Treatment Period in ACQ-5 (Asthma Control Questionnaire, 5-item Version)

• 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:
  • AZD5069 45 mg BID: 54.1% (72/133) versus 48.9% (69/141) on control; risk difference 5.2 percentage points (95% CI -6.6 to 17.0), risk ratio 1.11 (0.88–1.39); unadjusted two-proportion z-test p = 0.389.
  • AZD5069 15 mg BID: 65.7% (88/134) versus 48.9% (69/141) on control; risk difference 16.7 percentage points (95% CI 5.2 to 28.3), risk ratio 1.34 (1.09–1.65); unadjusted two-proportion z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between AZD5069 45 mg BID and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for AZD5069 15 mg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Patients Presenting Improvement From Baseline to End of Treatment Period in AQLQ(S) (Asthma Quality of Life Questionnaire Standardised Version) Overall Score

• 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:
  • AZD5069 45 mg BID: 47.0% (62/132) versus 44.6% (62/139) on control; risk difference 2.4 percentage points (95% CI -9.5 to 14.2), risk ratio 1.05 (0.81–1.36); unadjusted two-proportion z-test p = 0.696.
  • AZD5069 15 mg BID: 51.5% (68/132) versus 44.6% (62/139) on control; risk difference 6.9 percentage points (95% CI -5.0 to 18.8), risk ratio 1.15 (0.90–1.48); unadjusted two-proportion z-test p = 0.255.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between AZD5069 45 mg BID 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 AZD5069 15 mg BID and the control. The interval gives the range of effects that remain compatible with the data.

The registered secondary outcomes cover several kinds of information: asthma-specific hospital or intensive care admissions, lung function, asthma control, quality of life, and oral corticosteroid use related to worsening symptoms. The posted secondary results do not form a single consistent pattern across these different measures. Some comparisons show numerical differences between groups, while others are compatible with little or no difference under the reported uncertainty. They add context but do not replace the primary severe-exacerbation analysis.

The primary result itself has a discrepancy between the sponsor’s reported analysis and simple recalculation. Secondary findings should therefore be read as supporting descriptive information, not as a way to resolve that discrepancy. Measures such as asthma control, quality of life, lung function, and hospital admission capture distinct aspects of disease and need not move in parallel with the rate of severe exacerbations.

There are many secondary outcomes and dose comparisons. Unless multiplicity is controlled, repeated testing increases the chance that some comparisons will appear notable by chance. The registry record does not report whether a multiplicity adjustment was used or identify a hierarchy for interpreting the secondary endpoints. For this reason, unadjusted secondary results carry less inferential weight than a prespecified primary analysis. The registry’s outcome list and reported secondary estimates are useful for understanding what was assessed, but individual apparent differences should not be treated as independent confirmation of a primary effect.

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

• Rate of Asthma-specific Hospital Admission/Intensive Care Unit Admissions During 6 Months
• Total Number of Days of Asthma-specific Hospital Admission/Intensive Care Unit Admissions
• Total Number of Days on Oral Cortecosteroids, Due to a Worsening of Asthma Symptoms
• Change From Baseline to 2 Weeks Measurement of Pre-bronchodilator FEV1
• Change From Baseline to 1 Month Measurement of Pre-bronchodilator FEV1
• Change From Baseline to 2 Months Measurement of Pre-bronchodilator FEV1
• Change From Baseline to 3 Months Measurement of Pre-bronchodilator FEV1
• Change From Baseline to 4 Months Measurement of Pre-bronchodilator FEV1

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish the reported primary outcome from the simple recalculations and clarify what each result can support.

What a rate measures

General explanation: an event rate relates the number of events to a period of exposure or observation. It can include recurrent events, so it differs from a binary outcome that classifies each participant as having or not having an event. The primary endpoint is labeled as exacerbations per 6 month. The registry reports least-squares mean rates for each arm, but the detailed model used to produce those means is not reported in the registry record.

What a rate ratio means

General explanation: a rate ratio compares the event rate in one group with the rate in a reference group. A value of 1 represents equal rates under that comparison; a value above 1 represents a higher rate in the first group, and a value below 1 represents a lower rate. A rate ratio does not directly state the number of participants who experienced an event. It also does not establish a causal explanation on its own; interpretation depends on the design and analysis.

The sponsor’s reported analyses are described as Poisson regression and report risk ratios for the AZD5069 groups versus placebo. The registry’s primary outcome measure is a rate, while the reported analysis parameter is named Risk Ratio. The exact model specification, offsets or exposure handling, covariates, and any other adjustments are not reported in the registry record. Those details matter because a model-based comparison can differ from a calculation using only posted group summaries.

Why Poisson modeling and dispersion matter

General explanation: Poisson regression is often used to model event counts, including rates when observation time is incorporated. A basic Poisson model has a particular relationship between the expected count and its variability. If the observed variability is greater than that relationship allows, over-dispersion may make standard errors too small and confidence intervals too narrow unless the analysis accounts for it. This is a general consideration, not evidence that over-dispersion occurred in this trial. The registry record does not report a dispersion assessment or any adjustment for it.

How to read confidence intervals and p-values

A confidence interval describes the range of values compatible with the data under the model and procedure used; it is not a guarantee that the true value lies within that particular interval. The sponsor reports 90% intervals for its risk ratios. For these comparisons, an interval containing 1 is compatible with no difference in rate ratio at the stated confidence level. The sponsor’s reported intervals contain 1 for all three dose comparisons. A p-value summarizes how unusual data at least as incompatible with the null hypothesis would be under the specified model, assuming that model and null hypothesis. It is not the probability that the null hypothesis is true.

Unadjusted recalculations use the posted summary statistics and do not reproduce the full sponsor analysis. Their different estimates, intervals, and p-values demonstrate why model details matter. The discrepancy is flagged in the record, so the sponsor’s analysis takes precedence for the trial’s reported inference. The registry record does not provide information sufficient to identify the source of the difference.

Multiplicity and secondary comparisons

When many outcomes, doses, or comparisons are examined, the chance of at least one apparently notable result can increase. Statistical procedures can account for this multiplicity, but whether such a procedure was prespecified or used is not reported in the registry record. The recalculated p-values are unadjusted and should not be treated as if they account for all comparisons. Secondary outcomes can be useful for describing the breadth of results, but should be interpreted with more caution when the analysis plan and multiplicity handling are not reported.

What the planning calculations represent

The registry’s planning illustrations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is a stated fraction of the observed effect. For outcomes other than time-to-event outcomes, the figures are participants per arm; time-to-event calculations instead report total events. These calculations are illustrations based on observed effects, not the trial’s original design assumptions. The original sample-size assumptions are not reported in the registry record. They are not observed power: they describe hypothetical future planning under the listed assumptions, not the probability that this completed trial detected an effect.

11. Confidence Intervals and Precision

The arm-level primary estimates have 90% confidence intervals. For 45 mg, the reported rate is 0.31 with an interval from 0.2 to 0.5; for 15 mg, it is 0.31 with an interval from 0.19 to 0.49; for 5 mg, it is 0.26 with an interval from 0.16 to 0.42; and for placebo, it is 0.2 with an interval from 0.12 to 0.33. These intervals show substantial uncertainty around each arm’s estimated rate. They overlap, but overlap between arm-level intervals is not a substitute for the interval from a direct comparison.

The sponsor’s direct comparisons are more relevant to the treatment-versus-placebo question. The 90% confidence intervals for the reported risk ratios are 0.98 to 2.49 for 45 mg, 0.95 to 2.46 for 15 mg, and 0.79 to 2.11 for 5 mg. Each contains 1, so the reported results are compatible with no difference as well as with differences in either direction. Their breadth indicates that the comparisons do not locate the rate ratio precisely.

The recalculated intervals are narrower and do not contain 1, but the analysis is flagged as discrepant from the sponsor’s own results. That difference is not a reason to select the more favorable estimate: the sponsor’s analysis takes precedence. The registry record does not report sufficient modeling details to explain the differing precision. The intervals quantify uncertainty under their respective methods; they do not account automatically for unreported sources of uncertainty, multiplicity, or missing-data handling.

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 an assumed effect into a hypothetical sample requirement under specified assumptions. For the outcomes in these rate and binary displays, the reported figures are participants per arm, not total participants across arms. The registry’s general note distinguishes these from time-to-event calculations, which report total events; the primary severe-exacerbation endpoint is not presented as a time-to-event outcome.

The listed 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 displayed scenarios include planning for 100%, 75%, and 50% of the observed effect. Smaller effects require more participants to detect under the same assumptions, which is why the planning values rise as the assumed effect becomes smaller.

The 80% power column describes a hypothetical design with an 80% chance of detecting the specified effect under the calculation assumptions if that effect is real. The 90% power column describes the corresponding hypothetical design with a 90% chance. Higher target power generally requires a larger sample for the same effect and assumptions. These values are not observed power for this completed study; they are planning illustrations and should not be compared with enrollment as if they were the trial’s original design target.

The registry record does not report the original sample-size justification or its design assumptions. The illustrations are calculated from observed effects, and observed effects can be unstable estimates. They should therefore be read as conditional planning examples, not as evidence that the study was or was not adequately designed.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 2.4000; treatment rate λ₁ = 3.7200 events per patient-year; follow-up T = 0.50 years.
2. n = (1.96 + 0.842)² × (1/2.4000 + 1/3.7200) / (0.50 × [ln(1.550)]²) = 56.0, rounded up to 57 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
lambda0 <- 2.4                      # control rate, events per patient-year
lambda1 <- 3.72                      # treatment rate
tt      <- 0.5                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^2), 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(1704495)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 57 (80% power), 76 (90% power)
 75% of observed effect: n per arm = 105 (80% power), 140 (90% power)
 50% of observed effect: n per arm = 246 (80% power), 329 (90% power)
Simulated power, Poisson counts, n = 57 per arm: 0.816
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.641

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

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses using Poisson regression for the primary comparisons. The reported risk ratios versus placebo are 1.56 for AZD5069 45 mg, 1.53 for 15 mg, and 1.29 for 5 mg. The corresponding 90% confidence intervals are 0.98 to 2.49, 0.95 to 2.46, and 0.79 to 2.11; the p-values are 0.119, 0.141, and 0.397.

Unadjusted recalculations from the posted summary statistics produce different estimates, intervals, and p-values. In particular, the recalculated intervals do not match the sponsor-reported intervals, and the recalculated p-values are smaller. The record flags this discrepancy. The sponsor’s own analysis takes precedence for interpretation of the trial’s reported comparison; recalculated values are a simple check based on summary statistics, not a corrected sponsor result.

The registry record does not explain why the results differ. It does not provide the full model specification or enough analysis detail to reproduce the sponsor’s method. The discrepancy should remain visible rather than being resolved by assuming an unreported modeling choice. Consequently, conclusions should be anchored in the sponsor-reported analysis and should acknowledge its uncertainty.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when statistical testing covers multiple doses, endpoints, or comparisons. Even if each test uses a conventional significance threshold, looking across many tests increases the chance of at least one result appearing notable by chance. This trial has three AZD5069 dose comparisons for the primary outcome and a broad set of secondary outcomes. The registry lists 42 outcome measures and 41 posted secondary outcomes.

The registry record does not report whether the sponsor adjusted for multiplicity, used a testing hierarchy, or designated particular secondary outcomes as confirmatory. The reported sponsor p-values are available, but the record does not describe a family-wise error or false-discovery procedure. The simple recalculated p-values are explicitly unadjusted. They should not be interpreted as if they accounted for the number of comparisons.

Information about missing data is also limited. The primary analysis population is called the full analysis set, but its operational definition is not reported in the registry record. The record does not describe the amount or pattern of missing outcome data, the method used to handle missing data, or whether sensitivity analyses were conducted. The analysis-set counts in the posted outcomes are smaller than the enrollment figure, but the reason for the difference cannot be inferred from those counts alone.

The registry identifies the study as randomized and triple-masked, but does not report the allocation procedure beyond randomization or which parties were masked. It also does not provide the detailed statistical plan needed to assess prespecification, model diagnostics, or analysis choices. These omissions limit the ability to judge how robust the reported comparisons are to alternative procedures. They do not establish that a particular problem occurred; they identify information not reported in the registry record.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: asthma (2.6%), pneumonia (1.9%), atrial fibrillation (1.3%), helicobacter gastritis (0.7%), salmonellosis (0.7%).

The registry reports serious adverse event counts and other adverse event counts by treatment group. Serious adverse events affected 14 participants in the AZD5069 45 mg group, 8 in the 15 mg group, 7 in the 5 mg group, and 13 in the placebo group. Other adverse events affected 86, 68, 74, and 96 participants, respectively. The corresponding numbers at risk are listed as 161, 153, 156, and 159 for both categories in their respective groups.

These are counts, not adjusted comparisons, and they do not by themselves show whether an event was caused by study treatment. The registry lists serious-event terms including ASTHMA at 2.6%, PNEUMONIA at 1.9%, ATRIAL FIBRILLATION at 1.3%, HELICOBACTER GASTRITIS at 0.7%, SALMONELLOSIS at 0.7%, and STREPTOCOCCAL SEPSIS at 0.7%. The record does not provide enough detail to interpret these term percentages as comparative risks.

Death counts are not reported in the registry record. The safety counts should be read as reported event information rather than as a complete assessment of comparative safety, especially because details about event definitions, follow-up in the optional extension, and statistical comparisons are not reported.

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

The registry results describe a randomized, placebo-controlled comparison of three AZD5069 doses added to background asthma treatment. For the primary outcome, the posted arm-level rates are numerically higher in each AZD5069 group than in the placebo group. The sponsor’s reported risk-ratio comparisons have 90% confidence intervals that include 1, and the registry flags a discrepancy between those analyses and simple unadjusted recalculations. The sponsor’s analysis takes precedence, while the discrepancy limits how confidently the posted summary statistics can be reconciled.

These results do not establish that AZD5069 increases or decreases severe exacerbations. The sponsor’s estimates remain uncertain, and the registry record lacks the analysis details needed to explain why recalculation produces different inference. Nor does the record support a broad conclusion about all asthma outcomes: secondary measures assess distinct features and are subject to multiplicity concerns whose handling is not reported.

The findings also do not establish that the study treatment caused or prevented any particular adverse event. The safety figures are event counts by group, without reported causal assessment or comparative safety analysis in the information available. Death counts are not reported in the registry record.

Interpretation is specific to this study’s population, treatment regimen, follow-up period, endpoint definition, and analysis. The trial record concerns patients with uncontrolled persistent asthma receiving medium to high dose inhaled corticosteroids and long-acting β2 agonists, with AZD5069 or placebo as add-on capsules. It does not answer questions about other populations, regimens, or durations. No treatment decision should be based on these statistics alone.

18. Why This Trial Matters Statistically

This trial illustrates why the statistical method matters especially when the endpoint is a recurrent-event rate. The arm-level rates and their intervals offer a descriptive picture, while a direct model-based comparison addresses the treatment-versus-placebo question. In this record, those views cannot be collapsed into a single simple recalculation: the sponsor’s Poisson regression results differ from the unadjusted rate-ratio calculations based on posted summaries.

The discrepancy is important because it changes the apparent uncertainty of the comparisons. The sponsor’s intervals include 1, while the recalculated intervals do not. Treating the recalculations as the decisive result would disregard the sponsor analysis and the registry’s explicit discrepancy flag. Conversely, reporting only arm-level rates without their comparison method would leave readers without the sponsor’s inferential results. A sound reading keeps both visible and gives precedence to the sponsor analysis.

The study also illustrates why statistical precision, multiplicity, and transparency should be considered together. A range of doses and secondary measures were assessed, yet the registry does not report multiplicity procedures or detailed missing-data handling. Planning illustrations based on observed effects can help communicate how sample requirements vary with the effect assumed, but they cannot reveal the original design rationale or show whether the completed study had a particular probability of success.

For clinical researchers and biostatisticians, the practical statistical lesson is to distinguish posted descriptive estimates, sponsor-model comparisons, and exploratory recalculations. They answer related but not identical questions, and their assumptions and uncertainty should not be conflated.

19. Limitations

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

A central limitation for interpreting the primary result is the reported discrepancy between the sponsor’s analyses and simple unadjusted recalculations. The record does not provide the full model specification or enough detail to determine why the results differ. The sponsor’s analysis takes precedence, but readers cannot independently reproduce it from the information reported.

The primary population is named as the full analysis set, without a definition of eligibility for that set. Reasons for the analysis counts, missing outcome data, and the procedures used to handle missingness are not reported in the registry record. Model diagnostics, adjustment variables, and the handling of exposure time are also not described in sufficient detail. These gaps limit assessment of assumptions for the rate analysis.

The record does not report the original sample-size justification, interim analyses, or multiplicity procedures. Consequently, the planning illustrations based on observed effects cannot be used to infer the trial’s original design rationale. The broad set of secondary outcomes increases the importance of knowing whether comparisons were prespecified and adjusted, but that information is not reported.

The registry describes an optional safety extension up to 6 months, but does not report enough detail to distinguish safety follow-up from the primary treatment-period analyses. Serious and other adverse event counts are listed, but death counts are not reported in the registry record, and the counts alone do not establish causality. Finally, results from this Phase II study apply to its stated population and regimen; the registry information does not establish how findings generalize beyond them.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Phase II Study to Evaluate the Efficacy, Safety and Tolerability of AZD5069 in Patients With Uncontrolled Persistent Asthma. — NCT01704495.
• Registry record last updated 2016-03-01; status last verified 2016-02.
• Results first posted 2016-03-01.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes NCT01704495 as a completed Phase II randomized, placebo-controlled, parallel-group study of AZD5069 added to medium to high dose inhaled corticosteroids and long-acting β2 agonists in patients with uncontrolled persistent asthma. It lists triple masking and an optional safety extension up to 6 months. The primary outcome was the rate of severe asthma exacerbations during treatment up to 6 months, analyzed in the full analysis set.

Posted arm-level estimates were 0.31, 0.31, and 0.26 exacerbations per 6 month for AZD5069 45 mg, 15 mg, and 5 mg, compared with 0.2 for placebo. Sponsor-reported Poisson regression comparisons had 90% confidence intervals including 1. Simple unadjusted recalculations differ, and the record flags this discrepancy; the sponsor’s analysis takes precedence.

The registry does not report enough detail about the analysis plan, missing data, multiplicity, or original sample-size assumptions to resolve these limitations. Secondary outcomes and adverse-event counts provide additional descriptive context but require cautious interpretation.