Study to Investigate the Efficacy of Symbicort® SMART.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Investigate the Efficacy of Symbicort® SMART. (NCT00839800), a randomized phase 3 study. The primary outcome is The Percentage of Participants Who Had Experienced Asthma Exacerbation(s) at the End of the Study.

2. Clinical Question

This is an active-comparator question: both groups received scheduled Symbicort, while the as-needed medication differed. The primary outcome therefore concerns the proportion of participants experiencing a defined exacerbation, not a count of all symptoms, medication use, or exacerbation events. The registry also lists lung-function measures, as-needed medication use, symptom measures, and other secondary outcomes. Those address related but distinct aspects of asthma during the treatment period; they do not replace the primary comparison.

3. Trial Design

The registry describes a completed, randomized, parallel-group, active-controlled, phase III study in people with asthma from 16 years of age. The study was multinational and used quadruple masking according to the registry record. Its official title describes it as double-blind; the record does not explain the masking terminology or identify the roles covered by quadruple masking. Enrollment was 2091. The listed study dates are 2009-02 for start and 2011-02 for primary completion.

The two groups shared the same scheduled treatment: Symbicort Turbuhaler 160/4.5 µg, one inhalation twice daily. In the Symbicort SMART group, Symbicort was also available as needed. In the active-comparator group, terbutaline Turbuhaler 0.4 mg was available as needed. The comparison therefore focuses on the strategies for additional, as-needed treatment within a regimen that included scheduled Symbicort in both groups.

The primary outcome was assessed at week 52 and expressed as the percentage of participants who had experienced asthma exacerbation(s) by the end of the study. The registry defines exacerbation through deterioration in asthma leading to oral glucocorticosteroid treatment, hospitalization, or emergency room treatment. It identifies the efficacy population as the FAS, in line with the ICH E9 guideline, but does not describe the analysis procedures in detail.

The registry lists 13 outcome measures and 12 secondary outcomes. Numerical summaries are available for the primary outcome and for selected secondary measures. The record does not report the original sample-size justification, allocation ratio, details of treatment adherence, or a fuller account of how the masking and randomization procedures were implemented.

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: The study started with an enrolment visit, Visit 1, 1-7 days prior to Visit 2 (run-in). At Visit 2 patients had to have a reversibility of ≥12% relative to baseline and their pre-bronchodilatory Forced expiratory volume in one second (FEV1) had to be ≥50% of the predicted normal value.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis set for efficacy was based on the full analysis set (FAS) in line with the ICH E9 guideline.

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 The Percentage of Participants Who Had Experienced Asthma Exacerbation(s) at the End of the Study, measured over week 52.

The primary endpoint is the percentage of participants who had experienced one or more asthma exacerbations by week 52. It is a participant-level binary outcome: each participant either met the registry definition during the stated period or did not. The definition requires worsening asthma leading to oral glucocorticosteroid treatment, hospitalization, or emergency room treatment. It does not count symptom fluctuations that fail to meet those criteria as primary events.

This endpoint is useful because it captures episodes of worsening asthma that led to specified forms of treatment or urgent care. Reporting a percentage makes the comparison interpretable as the proportion of participants affected, rather than as an average symptom score or a total event count. It also means that participants with multiple exacerbations are represented as having experienced an exacerbation, not as contributing multiple participants to the percentage.

The registry identifies week 52 as the timeframe and says the efficacy analysis was based on the FAS in line with the ICH E9 guideline. Further operational details, including how incomplete follow-up or missing endpoint information was handled, are not reported in the registry record. The endpoint therefore describes the registry’s defined event and timeframe, while the available record does not fully document every analytic decision involved in estimating the percentages.

7. Results Posted in the Registry

• Symbicort+Terbutaline As Needed: 22.0% (229/1042) versus 16.0% (168/1049) on control; risk difference 6.0 percentage points (95% CI 2.6 to 9.3), risk ratio 1.37 (1.15–1.64); unadjusted two-proportion 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.

Morning Peak Expiratory Flow (PEF)

• 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 deviations.
• Result:
  • Symbicort+Terbutaline As Needed: mean 324.70 versus 331.80 on control; difference -7.10 (95% CI -15.91 to 1.71), standardized effect d = -0.07; z-test p = 0.114.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Symbicort+Terbutaline As Needed and the control. The interval gives the range of effects that remain compatible with the data.

Evening PEF

• 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 deviations.
• Result:
  • Symbicort+Terbutaline As Needed: mean 327.80 versus 334.20 on control; difference -6.40 (95% CI -15.28 to 2.48), standardized effect d = -0.06; z-test p = 0.158.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Symbicort+Terbutaline As Needed and the control. The interval gives the range of effects that remain compatible with the data.

Use of As-needed Medication

• 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 deviations.
• Result:
  • Symbicort+Terbutaline As Needed: mean 1.46 versus 1.21 on control; difference 0.25 (95% CI 0.12 to 0.38), standardized effect d = 0.17; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Symbicort+Terbutaline As Needed than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover different aspects of asthma, including peak expiratory flow and use of as-needed medication. Their overall pattern is not identical: the PEF mean contrasts point in one direction but have intervals that include no difference, while the medication-use contrast has an interval that excludes no difference and points in the other direction. The primary outcome concerns the percentage of participants experiencing a defined exacerbation, so these secondary measures are related to the clinical question but are not interchangeable with it.

The registry lists 12 secondary outcomes, while numerical summaries in the record describe three secondary measures. The registry does not list reported analyses for those outcomes. That makes the available summaries useful for describing observed group patterns, but the record does not establish how the secondary comparisons were prespecified, modeled, or interpreted in the sponsor’s analysis.

Unadjusted secondary results carry less weight than a prespecified primary comparison when many outcomes may be examined. In general, testing multiple outcomes without accounting for multiplicity raises the chance of obtaining at least one apparently noteworthy result by chance. The registry does not report a multiplicity procedure or hierarchy for interpreting secondary outcomes. A small unadjusted p-value on a secondary measure should therefore be considered alongside the number of outcomes, the direction and precision of the estimate, and whether it is consistent with the primary question.

Secondary outcomes can add context, especially when they describe function or medication use that the primary event endpoint does not capture. They do not independently confirm the primary finding merely because some estimates have a particular direction. Their interpretation is strongest when supported by a prespecified analysis plan and clear reporting of missing data and multiplicity, details that are not reported in the registry record.

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

• Number of Asthma Exacerbations
• Morning Peak Expiratory Flow (PEF)
• Evening PEF
• Forced Expiratory Volume in One Second (FEV1)
• Use of As-needed Medication
• Asthma Symptom Score
• Nights With Awakening(s) Due to Asthma Symptoms
• The Percentage of Participants Who Had Experienced First Mild Asthma Exacerbations

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: an individual either experienced a qualifying asthma exacerbation by week 52 or did not. A percentage summarizes the share of the analysis population meeting that definition. For a comparison of two such proportions, an absolute risk difference describes the subtraction of one group’s proportion from the other’s. The sign identifies the direction of the contrast, provided the group order is stated. Here, the reported recalculation uses the terbutaline-as-needed group relative to Symbicort SMART, and the positive estimate corresponds to the higher observed percentage in the comparator group.

The posted comparison gives a risk difference of 0.060 and a 95% confidence interval from 0.026 to 0.093. In general, a confidence interval is a range generated by a statistical procedure that reflects uncertainty in an estimate under its assumptions. It is not a range containing a fixed proportion of individual outcomes, and it is not the probability that the true effect lies in the particular interval. An interval that excludes zero indicates that zero difference is not among the values supported by that interval procedure at its stated confidence level. It does not settle questions about bias, missing data, or how the analysis was selected.

The unadjusted p-value for the primary comparison is < 0.001. In general, a p-value measures how unusual the observed data, or more extreme data, would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. The registry does not report a full inferential analysis or adjusted p-value; the comparison statistics are recalculated from posted summaries. The registry’s own analysis would take precedence if a discrepancy were identified, but the record flags no discrepancy.

The registry also lists a relative risk and an odds ratio for the primary comparison. These are relative measures, whereas the risk difference is an absolute measure. Relative measures compare proportions or odds in relation to one another; the risk difference describes the gap between the group proportions on the outcome scale. Each emphasizes a different aspect of the contrast. The absolute measure can be read alongside the two arm percentages without converting it into a new percentage-point value.

The secondary lung-function and medication-use measures are continuous outcomes summarized by means and standard deviations. A mean difference compares group averages, with the sign indicating which average is higher according to the stated group order. A confidence interval for a mean difference describes uncertainty about that average contrast. If such an interval includes zero, the data are compatible with no difference as well as with values on either side of zero under the interval’s assumptions.

Standard deviation describes variation among observed participant measurements; it is not the uncertainty in the estimated mean. The standard error, by contrast, describes sampling uncertainty in an estimate. In general, greater variability can make a group contrast less precise if other aspects of the data are held constant. The secondary summaries include standard deviations, and the recalculations use the posted group summaries. The registry does not list reported sponsor analyses for these secondary outcomes.

Planning calculations use the observed effect as a reference and illustrate the number of participants per arm associated with selected fractions of that effect under stated assumptions. In general, smaller target effects require more information to detect reliably when other assumptions remain unchanged. The posted planning calculations use equal allocation, a two-sided significance level of 0.05, and a normal approximation. They are planning illustrations based on observed estimates, not a reconstruction of the trial’s original design process. The original sample-size assumptions are not reported in the registry record.

Multiplicity arises when several outcomes or comparisons are tested. In general, the more tests that are considered, the greater the chance that at least one result appears unusual by chance if no adjustment or prespecified testing strategy is used. The registry lists multiple secondary outcomes, but a multiplicity plan is not reported in the registry record. Unadjusted secondary p-values therefore describe individual comparisons without establishing that the overall family of tests was controlled.

In general, over-dispersion matters when a count outcome varies more than an assumed probability model allows, because standard errors and confidence intervals based on an overly restrictive model may be too small. The primary endpoint is reported as a percentage of participants, not a count-rate analysis, and the registry does not describe an over-dispersion analysis. No inference about such a procedure can be made from the record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.060, with a 95% confidence interval from 0.026 to 0.093. The estimate is positive for the stated comparison of the terbutaline-as-needed group relative to Symbicort SMART. Both limits are on the same side of zero, so the interval indicates a directionally consistent contrast under the assumptions of the recalculation. The width of the interval also shows that the estimate is not a single exact value: a range of effect sizes remains compatible with the data and method.

In general, confidence intervals communicate precision as well as direction. A narrower interval indicates less sampling uncertainty under the model, while a wider interval leaves more uncertainty about the size of the contrast. An interval does not account automatically for systematic bias, incomplete outcome ascertainment, selective reporting, or unreported analytic decisions. Those issues need information beyond the interval itself.

The continuous secondary outcomes have their own mean-difference intervals. The intervals for morning and evening peak expiratory flow include zero, whereas the interval for use of as-needed medication does not. This pattern is consistent with greater uncertainty about the direction of the PEF average contrasts than about the medication-use contrast, according to the posted recalculations. The intervals concern group averages, not the range of individual participant measurements.

These intervals are unadjusted recalculations from posted summaries. They should be read as estimates of precision for the stated comparisons, not as a substitute for an analysis plan or for any sponsor analysis that is not reported in the registry record. The registry identifies the FAS for the primary efficacy analysis, but does not detail how missing data were treated; that limits how completely the interval’s assumptions can be evaluated.

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 are participants per arm for 80% power and participants per arm for 90% power. The outcomes in these planning illustrations are not time-to-event outcomes, so the figures refer to participants per arm rather than total events. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is specified as a fraction of the observed effect.

The 80% power column describes the number of participants per arm that the planning calculation associates with an 80% chance of detecting the specified target effect under its assumptions, if that effect is real. The 90% column makes the analogous illustration for 90% power. These are design-planning concepts: power is the probability of detecting an effect of a given size under a specified model and significance threshold. It is not the probability that a study result is true.

Rows for planning for 100% of the observed effect use the observed effect as the target. Rows for planning for 75% or 50% use smaller target effects. Smaller effects are harder to distinguish from random variation, so the planning calculations require more participants per arm to attain the same stated power. This relationship applies under the listed assumptions; it does not guarantee that a future trial will achieve its target.

The calculations are illustrations based on the observed effect, not the trial’s original design justification. The trial’s own sample-size assumptions are not reported in the registry record. These figures are not observed power: observed power is not a useful substitute for interpreting the estimated effect and its confidence interval after a study has been completed.

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 = 0.160; treatment proportion p₁ = 0.220; average p̄ = 0.190.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5548 = 1.0873.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5531 = 0.4655.
4. n = (1.0873 + 0.4655)² / (0.0596)² = 678.4, rounded up to 679 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 <- 0.160152526215443                          # control proportion
p1 <- 0.219769673704415                          # 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(839800)
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 = 679 (80% power), 908 (90% power)
 75% of observed effect: n per arm = 1,171 (80% power), 1,567 (90% power)
 50% of observed effect: n per arm = 2,551 (80% power), 3,414 (90% power)
power.prop.test: 678.4 
Simulated power at n = 679 per arm: 0.798 (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. Multiplicity, Missing Data and Analysis Populations

The registry lists 13 outcome measures, including 12 secondary outcomes. Multiple outcomes create a multiplicity issue: if many hypotheses are tested, the chance of at least one apparently unusual result can increase even when there is no underlying effect. A prespecified hierarchy, adjustment method, or other strategy can help control how the collection of tests is interpreted. Such a strategy is not reported in the registry record.

The posted comparison statistics are unadjusted recalculations from summary data. The primary p-value is therefore an unadjusted value, and the secondary p-values are also unadjusted. The record does not report whether the sponsor used a multiplicity adjustment, which outcomes were included in any testing family, or whether secondary results were intended to be confirmatory or descriptive. No adjusted interpretation should be inferred from the posted values.

The registry identifies the FAS in line with the ICH E9 guideline as the population for the primary efficacy analysis. It does not give further information on how the FAS was operationalized, whether all randomized participants contributed to the endpoint summary, or how missing outcome data were handled. The record also does not describe sensitivity analyses for missingness, imputation methods, or treatment of protocol deviations. These details matter because estimates can depend on which participants and observations are included and on assumptions about unavailable outcomes.

The number of analyses reported in the registry is zero, and the listed reported analyses are empty. Thus the registry record does not provide a full statistical analysis narrative against which to check the recalculations. Interim analyses, stopping rules, and the trial’s original statistical plan are not reported in the registry record. Their absence from the record does not establish that they were or were not used; it means their role cannot be evaluated from the available information.

15. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: asthma (3.0%), pneumonia (0.4%), gastroenteritis (0.3%), abdominal pain (0.3%), traumatic brain injury (0.2%).

The registry lists serious adverse events for 41 participants in the Symbicort SMART group, with 1049 at risk, and for 74 participants in the Symbicort-plus-terbutaline-as-needed group, with 1042 at risk. It also lists other adverse events for 279 and 293 participants, respectively, with the same group-specific at-risk counts. These are descriptive safety counts; they should not be treated as a causal comparison without information about definitions, ascertainment, follow-up, and analysis methods.

The listed serious-event terms include asthma at 3.0%, pneumonia at 0.4%, gastroenteritis at 0.3%, abdominal pain at 0.3%, traumatic brain injury at 0.2%, and type 2 diabetes mellitus at 0.2%. The registry record does not specify the denominator behind these term percentages in the information summarized for this comparison, so they should be read as listed rather than converted into participant counts. Deaths are not reported in the registry record.

Serious adverse events and the primary exacerbation endpoint are not the same measure. The primary endpoint has a stated definition and week-52 timeframe; the safety summary is a separate description of adverse events. Neither the counts nor the term percentages alone establish whether a treatment caused an event.

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

The posted primary summaries show a lower percentage of participants with a qualifying asthma exacerbation in the Symbicort SMART group than in the group using terbutaline as needed. The unadjusted recalculated risk difference is positive when expressed as comparator minus Symbicort SMART, and its confidence interval does not include zero. The unadjusted p-value is < 0.001. Together, these statistics indicate a clear observed contrast for the registry-defined endpoint, with uncertainty about its exact size.

This result applies to the trial’s population, treatment strategies, endpoint definition, and week-52 timeframe. It does not establish how outcomes would compare in populations or settings not described by the registry record. Nor does the primary endpoint capture every aspect of asthma: it focuses on qualifying exacerbations and does not by itself summarize lung function, daily symptoms, all medication use, or each participant’s experience.

The trial compared two active strategies that both included scheduled Symbicort. The contrast is specifically between additional Symbicort as needed and terbutaline as needed, not between Symbicort and no treatment. The registry’s results should therefore be interpreted as a comparison of those treatment regimens rather than as an isolated effect of a single drug independent of the rest of the regimen.

The record does not provide a full statistical analysis plan, details of missing-data handling, multiplicity procedures, or the original sample-size justification. The reported comparison statistics are unadjusted recalculations from posted summaries, and no sponsor analyses are listed. These gaps limit assessment of analytic robustness. The results describe the posted data; they are not medical advice, a guarantee of an individual outcome, or proof about effects beyond the study’s defined comparison.

17. Why This Trial Matters Statistically

This trial is statistically informative because its primary endpoint is defined in participant-level terms and reported as a percentage at a specified follow-up point. The comparison also reports an absolute risk-difference estimate with a confidence interval, allowing the direction and precision of the group contrast to be considered together rather than relying only on a p-value.

The randomized, parallel-group, active-controlled design addresses a practical contrast between two regimens with the same scheduled Symbicort and different as-needed medications. That shared background treatment helps define what the result does and does not compare. The age range, study timeframe, masking description, and named efficacy population provide important context for interpreting the estimates.

The record also illustrates why statistical significance is not a complete interpretation. A small unadjusted p-value does not describe the size of the effect, the relevance of the endpoint, or the potential influence of missing data and analysis choices. Confidence intervals and the endpoint definition supply additional context, while the absence of a reported multiplicity plan and full analysis details limits evaluation of the broader set of outcomes.

Finally, the planning illustrations show how sample-size requirements depend on the effect a future study aims to detect. They are based on observed effects and explicit planning assumptions, not the trial’s original design rationale. Separating those planning calculations from the observed trial results helps avoid treating a retrospective illustration as evidence about the trial’s intended power.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several details needed for a fuller appraisal are not reported in the registry record. These include the original sample-size justification and assumptions, a detailed statistical analysis plan, procedures for handling missing primary outcomes, and sensitivity analyses. The record identifies the FAS for the primary efficacy analysis but does not explain how that population was defined or how incomplete follow-up was addressed.

The registry lists multiple secondary outcomes, but does not report a multiplicity strategy, an outcome hierarchy, or sponsor analyses for the secondary comparisons. The available unadjusted recalculations should therefore be treated as descriptive evidence for individual comparisons rather than as a complete confirmatory analysis across all outcomes. The summary also does not document interim analyses or stopping rules.

The record states that masking was quadruple, while the official title describes the study as double-blind. It does not explain the terminology or identify which study roles were masked. It also does not provide details on adherence, treatment discontinuation, protocol deviations, or the extent of outcome ascertainment. These omissions do not demonstrate that such procedures were absent; they restrict what can be assessed from the registry information.

The primary endpoint is a specific treatment- or acute-care-defined exacerbation. It may not reflect all changes in asthma symptoms or function. Safety information is presented as event counts and selected term percentages, without a detailed account of definitions or comparative safety analyses. The results should consequently be interpreted within the limits of the registered outcome definitions and available summaries.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study to Investigate the Efficacy of Symbicort® SMART. — NCT00839800.
• Registry record last updated 2012-11-30; status last verified 2012-11.
• Results first posted 2012-11-30.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT00839800 is a completed randomized, parallel-group, active-controlled phase III study of Symbicort SMART versus scheduled Symbicort with terbutaline as needed in people with asthma from 16 years of age. The registry lists enrollment of 2091, quadruple masking, and a week-52 primary endpoint: the percentage of participants experiencing an asthma exacerbation defined by oral glucocorticosteroid treatment, hospitalization, or emergency room treatment.

The posted primary summaries are 16.0% for Symbicort SMART and 22.0% for Symbicort plus terbutaline as needed. The unadjusted recalculated risk difference is 0.060, with a 95% confidence interval from 0.026 to 0.093 and p < 0.001. The registry identifies the FAS for primary efficacy, but does not report a full analysis plan, missing-data procedures, or multiplicity approach. Secondary outcomes and adverse-event summaries provide additional context but require separate, cautious interpretation.