A Study in Asthma Patients to Evaluate Efficacy, Safety and Tolerability of 14 Days Once Daily Inhaled Interferon Beta-1a After the Onset of Symptoms of an Upper Respiratory Tract Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study in Asthma Patients to Evaluate Efficacy, Safety and Tolerability of 14 Days Once Daily Inhaled Interferon Beta-1a After the Onset of Symptoms of an Upper Respiratory Tract Infection (NCT02491684), a randomized phase 2 study. The primary outcome is Proportion of Patients With a Severe Asthma Exacerbation During 14 Days of Treatment.

2. Clinical Question

The trial focused on a period when respiratory infection symptoms could precede worsening asthma. Its primary endpoint counted patients whose severe exacerbation began during treatment, rather than measuring symptom change alone. The registry’s definition required worsening asthma symptoms and specified qualifying events involving systemic corticosteroids, an unscheduled or emergency visit requiring systemic corticosteroids, or hospitalisation requiring systemic corticosteroids.

The comparison is an evaluation of an assigned treatment strategy in this trial population and timeframe. It does not, by itself, answer whether the same results apply to patients without asthma, to other respiratory infections, or to treatment outside the recorded 14-day regimen. The posted primary results describe the observed group counts and a comparison estimate with uncertainty; they do not establish that either treatment prevents or causes exacerbations.

3. Trial Design

The registry identifies NCT02491684 as a completed, randomized, double-blind, placebo-controlled, parallel-group, multicentre Phase IIa study sponsored by AstraZeneca. The record lists an enrollment of 121 and gives trial start and primary completion dates of 2015-07-21 and 2016-11-24. The interventions were inhaled interferon beta-1a and matching placebo, each administered once daily for 14 days.

The primary endpoint concerned severe asthma exacerbations with onset during the 14-day treatment phase. The reported treatment groups included 61 participants in the AZD9412 arm and 60 in the placebo arm. The primary analysis population was the intention-to-treat set as defined in the registry: randomized patients who received at least one dose of investigational product and had some post-dose data available. The registry record does not report further details on randomization procedures, allocation concealment, or the blinding procedures used to maintain masking.

The registry also lists secondary outcomes concerning severe and moderate exacerbations, time to first exacerbation, exacerbation duration, asthma control, symptom scores, night-time awakening, and reliever medication use. The recorded time-to-event follow-up extended to 30 days after randomisation for the listed time-to-event outcomes, while the primary outcome covered the treatment phase. The record includes 15 outcome measures and 33 analyses. The original sample-size justification and the trial’s planned analysis details beyond the posted analyses are not reported in the registry record.

Randomization and masking are relevant design features because they aim to reduce systematic differences between groups and influence of treatment knowledge. A parallel-group design assigns participants to one group for the comparison. These design features support interpretation of the comparison, but they do not remove uncertainty arising from the relatively limited observed number of primary events or from incomplete reporting of analysis details.

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: 349 patients enrolled (signed informed consent) and 228 were not randomised. 121 patients met randomisation criteria and entered the pre-treatment phase. Patients were treated after developing symptoms of an upper respiratory tract infection (URTI) if they met all the inclusion criteria and none of the exclusion criteria for the treatment phase.

Pre-treatment Phase

Treatment Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Intention to treat (ITT) analysis set consisted of all randomised patients who received at least 1 dose of investigational product and had some post-dose data available.

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 of Patients With a Severe Asthma Exacerbation During 14 Days of Treatment, measured over Day 1 - 14 of the treatment phase..

The primary endpoint was the number of participants with a severe asthma exacerbation beginning during Day 1 to 14 of the treatment phase. The registry expressed the endpoint as a count in each treatment group and defined severe exacerbation as worsening asthma symptoms accompanied by one or more qualifying events. These included use of systemic corticosteroids for at least 3 consecutive days, a temporary increase of at least 2-fold in a stable oral corticosteroid background dose, an unscheduled or emergency visit due to asthma symptoms requiring at least 1 dose of systemic corticosteroids, or in-patient hospitalisation due to asthma requiring at least 1 dose of systemic corticosteroids.

This endpoint is clinically oriented because it captures worsening that meets specified treatment or healthcare-use criteria, rather than relying only on a symptom score. Counting participants with an event provides a direct comparison of how often the defined outcome occurred in each group during the stated treatment window. It also reduces multiple events in one participant to the participant-level outcome for this primary measure.

In the posted results, 7 participants in the AZD9412 group and 5 in the placebo group had a severe exacerbation. The registry does not provide additional component-level counts showing which qualifying criterion applied to each participant. The endpoint’s definition therefore gives the threshold for an event, while the posted group counts do not describe the detailed clinical course or severity within that definition.

7. Results Posted in the Registry

• AZD9412: 11.5% (7/61) versus 8.3% (5/60) on control; risk difference 3.1 percentage points (95% CI -7.5 to 13.8), risk ratio 1.38 (0.46–4.10); unadjusted two-proportion z-test p = 0.563.

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.

Time to First Severe Asthma Exacerbation During 30 Days Following Randomisation

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • AZD9412 vs Placebo: hazard ratio 1.30 (95% CI 0.45–3.77), reported p = 0.634 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between AZD9412 vs Placebo and the control. The interval gives the range of effects that remain compatible with the data.

Time to First Moderate Asthma Exacerbation During 30 Days Following Randomisation

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • AZD9412 vs Placebo: hazard ratio 1.05 (95% CI 0.07–16.78), reported p = 0.973 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between AZD9412 vs Placebo and the control. The interval gives the range of effects that remain compatible with the data.

AUC for Change in Daytime and Night-time Reliever Medication Use From Baseline up to 14 Days

• 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:
  • AZD9412: mean -0.12 versus -0.67 on control; difference 0.55 (95% CI -0.75 to 1.85), standardized effect d = 0.17; z-test p = 0.408.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between AZD9412 and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning exacerbations, asthma control, symptoms, night-time awakening, and reliever medication use. The available reported analyses do not form a precise or consistent pattern of separation between AZD9412 and placebo: the time-to-event estimates have broad confidence intervals, and the reliever-medication estimate also includes no difference. The registry does not provide numerical results for every listed secondary outcome, so no conclusion about those unreported outcomes can be drawn from the record.

These secondary measures address related but distinct questions from the primary endpoint. Time to first event considers when an event occurred; medication-use and symptom measures assess other aspects of asthma during follow-up. Their results can add context, but they do not overturn or independently establish the primary finding. In particular, a non-significant secondary result is not proof of no effect, while an isolated favorable result would need cautious interpretation.

When multiple outcomes are examined, the chance of observing an apparently notable result by chance can increase. A multiplicity strategy can account for this, but the registry record does not report whether adjustment or a hierarchical testing plan was used. Without that information, secondary results should carry less evidential weight than the designated primary result and should be viewed as exploratory context rather than definitive confirmation.

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

• Proportion of Patients With Severe Asthma Exacerbations Within 7 and 30 Days Following Randomisation
• Proportion of Patients With Moderate Asthma Exacerbation Within 7, 14 and 30 Days Following Randomisation
• Time to First Severe Asthma Exacerbation During 30 Days Following Randomisation
• Time to First Moderate Asthma Exacerbation During 30 Days Following Randomisation
• Duration of Moderate or Severe Exacerbations
• Change in Asthma Control From Baseline up to 30 Days as Measured by the Asthma Control Questionnaire (ACQ-6)
• AUC for Change in Daytime and Night-time Asthma Symptom Score From Baseline up to 30 Days
• Change in the Proportion of Night-time Awakening Using the ePRO Questionnaire From Baseline up to 30 Days

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: each participant either met the severe-exacerbation definition during the treatment phase or did not. For this kind of outcome, group proportions can be compared directly, and treatment effects can be expressed on different scales. The registry’s analysis reports a ratio of proportions from a log-binomial regression model. The simple recalculation reports a risk difference. These are distinct summaries: the ratio compares the proportions multiplicatively, whereas the difference describes the absolute separation between them.

What does the registry’s primary analysis estimate?

The reported log-binomial model gives a ratio of proportions of 1.29 for AZD9412 relative to placebo. A value at the null for this ratio would indicate equal proportions under the model. The confidence interval from 0.43 to 3.85 includes that null value and extends in both directions, so the estimate is compatible with a lower or higher proportion in the AZD9412 group. The p-value of 0.645 reflects the model-based test reported in the record. It is not a measure of the probability that the treatment effect is zero.

The recalculated risk difference is 0.031, with a 95% confidence interval from -0.075 to 0.138. For a risk difference, the null value is zero. The interval includes zero and also allows differences on either side of zero. The unadjusted p-value of 0.563 corresponds to this recalculation, not to the sponsor’s regression analysis. It should not replace the analysis specified and reported by the trial sponsor.

Why are there different estimates?

Different effect measures answer related but non-identical questions. A ratio of proportions describes relative contrast, while a risk difference describes absolute contrast. Regression can also account for model structure or covariates if they are included, although the registry does not report the model’s covariates. The recalculation is explicitly unadjusted and based on the posted summary counts. The sponsor’s own analysis takes precedence for interpretation of the trial’s planned or reported result; the recalculation is a supplementary way to describe the same group data.

For continuous outcomes, the registry reports a least-squares mean difference from ANCOVA for reliever medication use. ANCOVA is a regression-based method that can compare group means while adjusting for specified covariates, but the record does not identify those covariates. The sponsor reported a difference of 0.54, with a 95% confidence interval from -0.51 to 1.59 and p = 0.309. The unadjusted recalculation gives a mean difference of 0.55 and a wider confidence interval from -0.753 to 1.853. Because the reported analysis and recalculation differ in method, the sponsor’s result is the primary reference for that outcome as well.

How should the time-to-event analyses be read?

The registry reports Cox regression hazard ratios for time to first severe and moderate exacerbation. A hazard ratio compares the estimated event rates over follow-up, conditional on remaining event-free up to each time. It is not the same as a ratio of the total number of participants with events, and it does not directly state the difference in median time. The reported hazard ratio for time to first severe exacerbation was 1.30, with a 95% confidence interval from 0.45 to 3.77 and p = 0.634. The moderate-exacerbation hazard ratio was 1.05, with a 95% confidence interval from 0.07 to 16.78 and p = 0.973. The medians for these outcomes are not reported in the registry record.

Time-to-event analyses can use information about when events occur and can accommodate follow-up ending before an event for some participants, under assumptions about censoring and the model. The record does not report event counts, censoring details, or diagnostics for the Cox models. A confidence interval that spans a broad range indicates that the hazard ratio is estimated imprecisely. The unusually broad interval for the moderate outcome should be understood as limited information in the posted analysis, not as a stable estimate of a large effect.

Why can over-dispersion matter?

Over-dispersion is a general statistical concern when observed variability exceeds what a model assumes. If it is present and ignored, standard errors may be too small and confidence intervals too narrow. The primary endpoint is a binary participant count, and the registry reports a log-binomial model, but it does not report an over-dispersion assessment or adjustments. It is therefore not possible to say from the record whether over-dispersion was evaluated or whether it affected the inference. More generally, model assumptions matter because confidence intervals and tests depend on them.

The available estimates should be read alongside their outcome definitions, scales, and uncertainty. The reported analyses are not interchangeable, and secondary endpoints do not automatically carry the same evidential weight as the primary endpoint. Details of model specification, covariate selection, handling of missing values, and planned multiplicity control are not reported in the registry record.

11. Confidence Intervals and Precision

Confidence intervals describe a range of values reasonably compatible with the data and the statistical method, subject to the model assumptions. They are not guarantees that the true effect lies within the interval, and they do not show the probability that a particular value is correct. Their width is useful for judging how precisely an effect has been estimated.

For the primary outcome, the unadjusted risk-difference interval runs from -0.075 to 0.138. Because it includes zero, the data do not clearly distinguish a risk difference from no difference. It also spans effects in both directions, so the estimate does not rule out either a lower or a higher proportion with AZD9412. The sponsor’s ratio-of-proportions interval, 0.43 to 3.85, similarly includes the ratio null and is broad.

The secondary time-to-event intervals are also wide. The severe-exacerbation hazard-ratio interval is 0.45 to 3.77; the moderate-exacerbation interval is 0.07 to 16.78. These ranges indicate substantial imprecision and do not support a narrow conclusion about the size or direction of the associations. The reliever-medication confidence interval from the ANCOVA analysis, -0.51 to 1.59, includes zero as well.

Precision depends in part on the amount of information available, including the number and distribution of events, as well as on design and analysis choices. The registry lists relatively few primary events in each group, and the confidence interval reflects uncertainty about the treatment contrast. Statistical uncertainty is distinct from whether an effect would be clinically important; the record does not specify a threshold for clinical importance. The findings should therefore be interpreted as inconclusive rather than as proof of no effect or proof of a particular effect.

12. Planning a Similar Trial: Sample Size

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

The sample-size calculations are planning illustrations based on the observed effect, not the trial’s original design justification. The original design assumptions are not reported in the registry record. For outcomes other than time-to-event outcomes, the displayed figures are participants per arm. For time-to-event outcomes, the figures are total events. These quantities are not interchangeable: the time-to-event calculations concern event counts, not participants assigned to each arm.

The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect. The columns for 80% and 90% power describe the planning number associated with those target probabilities of detecting an effect of the assumed size under the stated assumptions, if that effect exists. They are not estimates of how likely this completed trial was to detect its effect.

Rows that plan for 75% or 50% of the observed effect assume a smaller target effect than the row based on 100% of the observed effect. Smaller effects are generally harder to distinguish from random variation, so they require more participants or events for the same target power. The figures should be used as conditional planning illustrations, not as evidence that a future study will achieve a particular result. This is not observed power.

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 = 0.083; treatment proportion p₁ = 0.115; average p̄ = 0.099.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4225 = 0.8280.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4219 = 0.3551.
4. n = (0.8280 + 0.3551)² / (0.0314)² = 1,417.7, rounded up to 1,418 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 <- 0.0833333333333333                          # control proportion
p1 <- 0.114754098360656                          # 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(2491684)
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 = 1,418 (80% power), 1,898 (90% power)
 75% of observed effect: n per arm = 2,432 (80% power), 3,255 (90% power)
 50% of observed effect: n per arm = 5,270 (80% power), 7,055 (90% power)
power.prop.test: 1417.7 
Simulated power at n = 1,418 per arm: 0.802 (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 sponsor’s primary analysis is the registry-reported log-binomial regression result: a ratio of proportions of 1.29, with a 95% confidence interval from 0.43 to 3.85 and p = 0.645. The recalculation from the posted group counts is an unadjusted risk difference of 0.031, with a 95% confidence interval from -0.075 to 0.138 and p = 0.563. These analyses use different effect scales and methods, so the estimates and p-values need not match.

The sponsor’s analysis takes precedence over the simple unadjusted recalculation when describing the trial’s own reported result. The recalculation is supplementary and helps express the comparison as an absolute difference based on the posted counts. Both analyses have confidence intervals that include their respective null values and are imprecise. Neither should be interpreted as demonstrating equivalence, and the recalculation should not be presented as a replacement for the registry-reported analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and lists multiple secondary outcomes and analyses. It does not report a multiplicity adjustment, a hierarchy for testing outcomes, or another strategy for controlling the overall chance of false-positive findings across analyses. This matters because repeated testing can increase the chance that at least one result appears statistically notable by chance. The posted secondary analyses should therefore be interpreted cautiously, particularly when considered individually.

The primary population is described as an intention-to-treat analysis set comprising all randomized patients who received at least one dose of investigational product and had some post-dose data available. This is the registry’s stated definition; it is not a complete account of how every randomized participant was handled. The record does not report the number excluded from this analysis set, reasons for exclusion, missing-data amounts by outcome, or methods used to handle missing values.

These omissions limit assessment of whether missing data could have influenced the estimates. Missingness can matter if the likelihood of having an outcome recorded is related to treatment or to the outcome itself. The record also does not describe sensitivity analyses for missing data, analysis-set definitions for each secondary outcome, or whether all analyses followed a prespecified plan. The trial’s original statistical analysis plan, sample-size justification, and any interim analyses are not reported in the registry record.

These reporting gaps do not establish that the analyses were inappropriate; they mean that the registry alone does not allow those methods to be assessed. The primary comparison remains interpretable as reported, but its context is incomplete, and secondary findings warrant particular restraint.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: asthma (4.9%).

The registry reports serious adverse events in 3 participants in the AZD9412 group and none in the placebo group. The top serious adverse event term listed is Asthma, at 4.9%. The record also reports other, non-serious adverse events affecting 27 participants in the AZD9412 group and 20 in the placebo group. These are descriptive counts and do not, on their own, establish that treatment caused an event or that the groups differ reliably in safety.

Deaths are not reported in the registry record. The record does not provide a complete breakdown of all adverse-event terms, their timing, severity, or relationship to study treatment. The serious-event figures should therefore be read as a limited summary of events recorded during the study, not as a complete safety assessment. Differences between observed counts can reflect chance as well as treatment-related effects, particularly when event counts are limited.

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

The trial’s posted primary results show 7 participants with a severe asthma exacerbation in the AZD9412 group and 5 in the placebo group during the treatment phase. The registry-reported analysis and the unadjusted recalculation both leave substantial uncertainty about the size and direction of the treatment contrast. The data do not establish a clear difference, but they also do not demonstrate that the treatments are equivalent.

The findings apply to the trial population, the recorded inhaled regimen, the treatment window, and the specified severe-exacerbation definition. They should not be extended automatically to other patient groups, dosing schedules, outcomes, or follow-up periods. The registry includes secondary measures, but many are not numerically reported in the record, and the available secondary estimates are imprecise.

A lack of statistical evidence for a difference is not the same as evidence that no clinically meaningful difference exists. Conversely, the observed counts alone do not show that AZD9412 increased risk. Interpretation depends on the uncertainty intervals, analysis methods, event definitions, and completeness of reporting, not only on which group had the larger observed count.

The safety information is also limited to the adverse-event summaries in the record. It does not establish causality, and deaths are not reported. Overall, the registry supports a cautious account: the primary comparison is inconclusive, the estimates are imprecise, and important details about analysis and outcome reporting are unavailable.

18. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be read together with its effect estimate and confidence interval, rather than by comparing event counts alone. The observed primary counts differ, but the interval around the comparison includes no difference and allows effects in either direction. The data therefore do not provide a precise estimate of the treatment contrast.

It also demonstrates that statistical conclusions depend on the scale of measurement. A ratio of proportions and a risk difference describe the same group comparison in different ways. The sponsor’s regression analysis is the principal reported result; an unadjusted recalculation can offer context but should not be substituted for it. Clear separation of these analyses prevents a supplementary estimate from being mistaken for the trial’s own model-based result.

The breadth of the secondary time-to-event intervals shows how limited event information can constrain inference. Multiple endpoints also make prespecification and multiplicity reporting important: without these details, secondary findings are harder to weigh and should not be treated as independent confirmation. Finally, the registry’s incomplete reporting of missing-data handling and analysis plans highlights why transparent statistical methods are essential for judging both the reliability and the limits of clinical trial evidence.

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.

The registry record does not report the original sample-size justification or the assumptions used when the study was designed. The planning illustrations based on observed effects cannot fill that gap. Details of randomization procedures, concealment, model covariates, and the full statistical analysis plan are also not reported in the registry record.

For the primary outcome, the record provides group counts and an analysis result but does not show the component-level breakdown of severe exacerbations or the number meeting each criterion. The intention-to-treat population definition requires post-dose data, but exclusions, missingness, and handling of unavailable outcomes are not described. These details limit assessment of how representative the analyzed population was of all randomized patients.

The record lists many secondary outcomes, yet it does not report numerical results for every listed outcome. The available time-to-event analyses have wide confidence intervals, and the median times are not reported. Multiplicity procedures and interim analyses are not reported, so the role of the secondary analyses in the original testing plan cannot be assessed.

The safety summary does not provide a full event-term listing, timing, treatment relatedness, or death counts. These reporting limits mean that the posted safety figures cannot serve as a complete evaluation of harms. The findings should be interpreted as a registry-based account of the available results, with uncertainty about both the effects and the unreported analytic details.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study in Asthma Patients to Evaluate Efficacy, Safety and Tolerability of 14 Days Once Daily Inhaled Interferon Beta-1a After the Onset of Symptoms of an Upper Respiratory Tract Infection — NCT02491684.
• Registry record last updated 2019-02-12; status last verified 2019-01.
• Results first posted 2019-01-15.
• 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

NCT02491684 was a completed randomized, double-blind, placebo-controlled, parallel-group Phase IIa study in patients with asthma after onset of upper respiratory tract infection symptoms. It compared once-daily inhaled AZD9412, described as interferon beta-1a, with matching placebo for 14 days.

The primary outcome was the proportion of participants with a severe asthma exacerbation during treatment. The registry reports 7 events in the AZD9412 group and 5 in the placebo group. The sponsor’s log-binomial analysis gave a ratio of proportions of 1.29, with a 95% confidence interval from 0.43 to 3.85 and p = 0.645. The result is imprecise and does not establish a difference between groups.

Secondary estimates are also uncertain, and the registry does not report all analysis details or numerical findings for every listed outcome. The record supports cautious interpretation of the primary and secondary results, with limitations in precision and reporting.