Evaluation of Efficacy on Exercise Tolerance of Symbicort (Budesonide/Formoterol) Compared to Placebo and Oxis in Patients With Severe COPD: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of Efficacy on Exercise Tolerance of Symbicort (Budesonide/Formoterol) Compared to Placebo and Oxis in Patients With Severe COPD (NCT00489853), a randomized phase 4 study. The primary outcome is Exercise Endurance Time (EET) at 75% of Peak Work Capacity With Cycle Ergometry 1 Hour Post-dose.

2. Clinical Question

3. Trial Design

This was a phase 4, randomized, quadruple-masked, crossover study of Symbicort, formoterol, and placebo in patients with severe COPD. Enrollment was 137. The registry lists the study as completed, with a start in 2007-07 and primary completion in 2008-08. AstraZeneca is named as the sponsor.

In a crossover design, participants receive more than one study treatment in a sequence, rather than remaining in a single parallel treatment group throughout. The registry lists three sequences, each containing Symbicort, formoterol, and placebo in a different order. The primary endpoint was measured at the end of each 1-week treatment period. This design can make within-person comparisons possible, because a participant may contribute measurements under different treatments. It also makes period and sequence structure relevant to analysis.

The primary endpoint description says that the sponsor calculated treatment means from individual patient data using a model with patient and period as fixed factors. Patients with only one EET value were excluded from that model, which required data from at least two periods. The registry record does not report the sponsor’s numerical model estimates, its complete statistical analysis plan, or the handling of sequence or carryover effects.

The arm-level summaries list 96 participants for Symbicort, 98 for formoterol, and 99 for placebo for the primary endpoint. These are treatment-level counts, not a statement that the crossover trial had three independent parallel groups. Participants could contribute data under multiple treatments, and the record does not give a complete account of missing observations across periods. The listed enrollment therefore should not be treated as the sample size for each treatment comparison.

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: Among 137 enrolled patients, 26 patients were not randomised (14 due to violation of inclusion/exclusion criteria, 2 due to adverse events, 1 due to development of study-specific discontinuation criteria, 7 due to voluntary discontinuation, 1 due to lost to follow-up, and 1 due to other reason.)

Treatment Period 1

Wash-out Period 1

Reasons for not completing this period:

Treatment Period 2

Wash-out Period 2

Reasons for not completing this period:

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 Exercise Endurance Time (EET) at 75% of Peak Work Capacity With Cycle Ergometry 1 Hour Post-dose, measured over Single measurement taken1 hour post-dose at the end of each 1-week treatment period.

The primary endpoint was exercise endurance time (EET), measured in seconds during cycle ergometry at 75% of peak work capacity. The measurement was taken 1 hour after dosing, at the end of each 1-week treatment period. Exercise endurance time captures how long a participant sustains exercise under a specified test workload. It is a functional measure, rather than a direct measurement of lung volume or airflow.

Using a fixed proportion of peak work capacity sets the exercise test relative to a participant’s capacity. That allows the endpoint to represent exercise tolerance under a defined workload, while recognizing that participants may have different peak capacities. The registry names exercise tolerance as a study objective and also lists lung function and symptoms as outcomes of interest.

Because this was a crossover study, EET could be measured for the same person during different treatment periods. Within-person comparisons can account for stable differences between participants, but valid analysis depends on the trial’s design and model. The sponsor’s endpoint description says its model included patient and period as fixed factors and required EET data from at least two periods. Numerical results from that sponsor model are not reported in the registry record. The displayed arm means and simple unadjusted comparisons describe the posted treatment-level summaries; they should not be mistaken for the sponsor’s crossover-model estimates.

7. Results Posted in the Registry

• Symbicort: mean 529.00 versus 406.00 on control; difference 123.00 (95% CI 26.46 to 219.54), standardized effect d = 0.36; z-test p = 0.013.
• Formoterol: mean 441.00 versus 406.00 on control; difference 35.00 (95% CI -48.52 to 118.52), standardized effect d = 0.12; z-test p = 0.411.

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.

Exercise Endurance Time (EET) at 75% of Peak Work Capacity With Cycle Ergometry 6 Hour Post-dose

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Symbicort: mean 463.00 versus 388.00 on control; difference 75.00 (95% CI -12.22 to 162.22), standardized effect d = 0.24; z-test p = 0.092.
  • Formoterol: mean 408.00 versus 388.00 on control; difference 20.00 (95% CI -62.52 to 102.52), standardized effect d = 0.07; z-test p = 0.635.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Symbicort 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 Formoterol and the control. The interval gives the range of effects that remain compatible with the data.

Forced Expiratory Flow (FEV1) Pre-dose

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Symbicort: mean 0.08 versus -0.05 on control; difference 0.13 (95% CI 0.07 to 0.19), standardized effect d = 0.59; z-test p = <0.001.
  • Formoterol: mean 0.06 versus -0.05 on control; difference 0.11 (95% CI 0.05 to 0.17), standardized effect d = 0.50; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Symbicort than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Formoterol than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Forced Vital Capacity (FVC) Pre-dose

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Symbicort: mean 0.06 versus -0.09 on control; difference 0.15 (95% CI 0.05 to 0.26), standardized effect d = 0.40; z-test p = 0.005.
  • Formoterol: mean 0.07 versus -0.09 on control; difference 0.16 (95% CI 0.05 to 0.27), standardized effect d = 0.42; z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Symbicort than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Formoterol than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists multiple secondary outcomes spanning exercise endurance, lung function, peak expiratory flow, sleep, breathlessness, and chest tightness. Numeric summaries in the posted secondary results include 6-hour EET, pre-dose FEV1, and pre-dose FVC. The pattern is not uniform across these outcome types: the 6-hour EET comparisons are less precise, while the listed lung-function comparisons have intervals that exclude zero under the simple unadjusted calculations. These results complement the primary question by describing exercise endurance at another time and changes in lung function.

They do not replace or directly validate the primary 1-hour EET result. EET and lung-function measures represent different outcomes, are measured on different scales, and may have different variability. A numerical pattern in one outcome cannot be treated as proof about another. The secondary results also come from a crossover study, while the simple recalculations do not incorporate the within-person covariance or the sponsor’s described patient-and-period model.

Each secondary comparison should be treated as exploratory unless the planned hierarchy and inferential procedures are known. Testing several outcomes and treatment contrasts increases the chance that at least one unadjusted result appears persuasive by chance. The registry record does not report a multiplicity adjustment or identify a confirmatory hierarchy for the secondary outcomes. Unadjusted p-values and confidence intervals therefore carry less confirmatory weight than results from a prespecified analysis plan with appropriate handling of multiple comparisons.

The record lists 29 posted secondary outcomes, but detailed estimates for all listed measures are not reported in the registry record. The absence of a numerical summary for an outcome should not be interpreted as evidence that the outcome showed no difference. Nor can selective availability of results be ruled out from these entries alone. The overall secondary pattern is best used to describe the range of measured outcomes and the uncertainty of the posted contrasts, not as a collection of independent tests establishing a broader conclusion.

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

• Exercise Endurance Time (EET) at 75% of Peak Work Capacity With Cycle Ergometry 6 Hour Post-dose
• Forced Expiratory Flow (FEV1) Pre-dose
• Forced Vital Capacity (FVC) Pre-dose
• Vital Capacity (VC) Pre-dose (Change From Pre-treatment to Treatment)
• Peak Expiratory Flow (PEF) Before Morning Dose
• Sleep Score
• Breathlessness Score
• Chest Tightness Score

9. Statistical Interpretation

10. Statistical Methods Explained

These results involve continuous outcomes, which are measurements that can take a range of numerical values. EET is recorded in seconds, while FEV1 and FVC are recorded in liters. A mean describes the average observed value in a treatment group. A standard deviation describes the spread of individual measurements around that group mean; it is not the uncertainty in the mean itself.

What does a mean difference represent?

A mean difference compares the reported mean for an active treatment with the mean for placebo. For the primary endpoint, the posted unadjusted comparison is 123.0 seconds for Symbicort versus placebo and 35.0 seconds for formoterol versus placebo. The sign indicates which mean is numerically larger in the stated ordering. These values are simple comparisons of treatment summaries, not estimates from the sponsor’s crossover model.

In a parallel-group study, treatment groups generally contain different people. In a crossover study, the same participant can contribute measurements under multiple treatments. Such repeated observations are related: a participant’s measurements across periods may be more alike than measurements from unrelated participants. An analysis that accounts for this relationship can use within-person information and should also reflect the trial’s period structure. The primary endpoint description states that the sponsor used patient and period as fixed factors. The registry record does not report the resulting model estimates, the model’s full specification, or whether other design effects were included.

Why is the crossover structure important?

A simple comparison of arm means and standard deviations does not contain the covariance between an individual’s measurements on different treatments. That covariance is relevant when estimating the variability of a within-person treatment contrast. The recalculated comparisons are therefore unadjusted summaries based on the posted treatment-level statistics; they do not recreate the sponsor’s model. In particular, the posted data do not permit reconstruction of the paired standard error or a complete crossover analysis.

Period can matter because participants may change over time regardless of treatment. The sponsor’s description names period as a fixed factor, but further details about sequence effects, carryover, washout, or how such issues were assessed are not reported in the registry record. Those details should not be inferred from the arm labels or treatment order alone.

How should the confidence interval be read?

A confidence interval gives a range of values reasonably compatible with the estimate under the method used. Wider intervals indicate less precision; narrower intervals indicate greater precision. For an unadjusted mean difference, an interval that includes zero is compatible with no difference as well as differences in either direction. An interval that lies entirely on one side of zero excludes zero under that particular calculation, but it does not by itself establish clinical importance or remove concerns about the analysis design.

The intervals reported for the recalculated comparisons use the posted group summaries. In this crossover study, they do not incorporate the within-person covariance or the sponsor’s patient-and-period model. Consequently, the interval’s conventional interpretation is conditional on the simple comparison method and should not be presented as the sponsor’s primary inferential result.

What does an unadjusted p-value say?

A p-value describes how unusual data at least as incompatible with a specified no-difference assumption would be, if that assumption and the analysis model were correct. It is not the probability that the no-difference assumption is true, and it is not a measure of the size or importance of an effect. The listed p-values are explicitly unadjusted. The registry record does not report whether the sponsor used an adjustment for multiple outcomes or comparisons, nor does it report the sponsor’s p-values for the primary endpoint model.

Multiple endpoints and comparisons create more opportunities for apparently notable results to arise by chance. Interpretation should therefore consider the outcome hierarchy, analysis plan, and multiplicity procedures. The registry lists multiple secondary outcomes, but the statistical plan and multiplicity procedure are not reported in the registry record.

What does the standardized effect describe?

The posted recalculations also include standardized effect estimates. A standardized effect expresses a mean difference relative to a pooled standard deviation, making the difference dimensionless and allowing comparisons across outcomes with different units. It is not a replacement for the original-scale difference: seconds or liters are often easier to relate to the measurement itself. Standardized values can also be sensitive to the variability of the study population and do not establish clinical importance.

The recalculated comparisons are simple, unadjusted calculations from posted summary statistics. They are not the sponsor’s reported analysis; no numerical sponsor analyses are reported in the registry record. No discrepancy between the posted summaries and these recalculations is identified. The interpretation remains limited by the crossover design and the absence of the sponsor model’s numerical results.

11. Confidence Intervals and Precision

For the primary 1-hour EET comparison, the Symbicort-versus-placebo mean difference is 123.0 seconds, with a 95% confidence interval from 26.46 to 219.5 seconds. The interval is wide relative to the point estimate, so the estimated size of the difference remains uncertain. It lies above zero under this unadjusted calculation, but it does not show the precision of the sponsor’s crossover-model estimate, which is not reported in the registry record.

For formoterol versus placebo, the mean difference is 35.0 seconds, with a 95% confidence interval from -48.52 to 118.5 seconds. The interval includes zero and allows for a range of possible differences in both directions. This means that the simple comparison is not precise enough to distinguish clearly between those possibilities.

A confidence interval is not a range containing every individual participant’s value. It describes uncertainty about an estimated group contrast under the calculation used. Here, the simple recalculations are based on treatment-level means and variability. Because participants crossed over between treatments, the within-person relationship in their measurements is important; that information is not captured by independent treatment summaries. The displayed intervals should consequently be read as uncertainty intervals for unadjusted comparisons, not as a replacement for a model that accounts for patient and period.

Precision and clinical relevance are separate questions. A narrow interval can still include effects that are unimportant, and a broad interval can include effects that might matter. The registry record does not state a threshold for a clinically meaningful EET difference. The intervals alone cannot answer that question, nor do they establish how results would generalize beyond the studied participants.

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 planning figures are illustrations based on the observed unadjusted effect, not the original trial’s design assumptions. The registry record does not report the original sample-size justification. For these continuous outcomes, each figure is the number of participants per arm, not a total number of events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario asks how many participants per arm would be needed to detect a stated fraction of the observed effect.

The 80% power column represents a planning target under which a study would have an 80% chance of detecting the specified effect if that effect were truly present and the assumptions held. The 90% power column uses a higher chance of detection as the planning target, and therefore generally requires more participants. These are hypothetical planning calculations, not observed power for this completed trial.

Rows planning for 100% of the observed effect use the full observed estimate as the target. Rows planning for 75% or 50% of the observed effect consider smaller effects. Smaller effects are harder to distinguish from ordinary sampling variation, so they require more participants for the same power target. The figures depend strongly on the observed effect used as the starting point; when that estimate is uncertain, the resulting planning illustration is uncertain as well.

The calculations assume equal allocation between two arms and use a normal approximation. They do not reproduce the study’s crossover design or the sponsor’s patient-and-period model. They should be read as a simple comparison-based illustration, not a proposed sample size for a future crossover study. The displayed curve uses the same planning logic and does not supply information about the trial’s original design rationale.

13. How the Sample Size Is Derived

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

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 123.000; pooled standard deviation σ = 342.791.
2. n = 2 × (1.96 + 0.842)² × 342.791² / 123.000² = 121.9, rounded up to 122 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 123                      # observed difference in means
sigma <- 342.790914988953                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(489853)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 122 (80% power), 164 (90% power)
 75% of observed effect: n per arm = 217 (80% power), 291 (90% power)
 50% of observed effect: n per arm = 488 (80% power), 653 (90% power)
power.t.test: 122.9 
Simulated power at n = 122 per arm: 0.794 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The study includes a primary endpoint, multiple secondary outcomes, and contrasts of two active treatments with placebo. Considering many outcomes and comparisons raises a multiplicity issue: even when no real treatment differences exist, some unadjusted results may appear unusual by chance. The registry record does not report a multiplicity adjustment, a testing hierarchy, or whether any secondary comparisons were intended as confirmatory. The listed unadjusted p-values should therefore be interpreted cautiously and should not be treated as if each were the sole planned test.

Important details about the analysis plan are also not reported in the registry record. These include the original sample-size justification, any interim analyses, the complete specification of the sponsor’s statistical model, and numerical results from that model. The endpoint description says that the sponsor’s model included patient and period as fixed factors and required data from at least two periods. It does not provide the model estimates or explain the handling of other possible crossover features, such as sequence or carryover effects.

The record does not fully describe analysis populations, including whether the primary analysis followed an intention-to-treat principle, a per-protocol definition, or another rule. It also does not give a complete account of missing data by participant and treatment period, how missing measurements were handled, or whether sensitivity analyses were conducted. The endpoint note does state that patients with only one EET value were excluded from the described model. The consequences of that exclusion cannot be assessed from the available information.

These gaps matter because crossover analyses rely on the pattern of repeated measurements and the assumptions used to handle incomplete periods. Treatment-level counts alone do not show how many participants contributed complete data across all periods, or whether missingness differed by treatment or sequence. Without the analysis plan and model output, the unadjusted recalculations can aid descriptive interpretation but cannot establish what the sponsor’s prespecified primary analysis concluded.

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: wrist fracture (1.0%), chronic obstructive pulmonary disease (1.0%).

The posted safety summaries give the number at risk and the number affected by serious and other adverse events for each treatment. For serious adverse events, the counts are 2 of 101 for Symbicort, 1 of 102 for formoterol, and 1 of 104 for placebo. For other adverse events, the counts are 4 of 101 for Symbicort, 3 of 102 for formoterol, and 6 of 104 for placebo. These are counts of participants affected in the listed groups; they do not describe event timing, duration, severity beyond the serious classification, or whether a participant experienced more than one event.

The registry also lists wrist fracture and chronic obstructive pulmonary disease among the top serious adverse-event terms, each reported as 1.0%. These terms do not by themselves establish that an event was caused by a treatment. The record does not report death counts, so deaths should not be interpreted as absent. Safety counts are descriptive, and the posted information does not support a detailed comparison of risk or a causal conclusion about treatment-related events.

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

The posted primary outcome summaries show that mean EET at 1 hour after dosing was numerically higher for Symbicort than for placebo, while formoterol’s mean was also numerically higher than placebo. The simple unadjusted Symbicort comparison has a confidence interval above zero; the formoterol comparison has an interval that includes zero and allows for differences in either direction. These statements describe the posted summaries and their uncertainty, not a clinical recommendation or a conclusion that a treatment does or does not work.

The distinction between the simple comparisons and the sponsor’s crossover analysis is important. Participants received treatments across different periods, and the sponsor’s endpoint description specifies a model with patient and period as fixed factors. Numerical output from that model is not reported in the registry record. Simple comparisons of treatment means do not account for the within-person covariance that can be central to crossover inference. They can summarize the direction and scale of the posted means, but they cannot stand in for the unavailable model results.

Statistical evidence and clinical importance are also distinct. A confidence interval describes uncertainty under a particular analysis, while clinical importance depends on whether the size of a difference matters in context. The registry record does not state a clinically meaningful threshold for EET. It is therefore not possible to classify the observed difference as clinically important based on these results alone.

The secondary results offer additional descriptions of exercise endurance and lung function, but multiple outcomes and unadjusted comparisons limit their confirmatory force. No complete multiplicity strategy or numerical sponsor analysis is reported. Safety summaries provide counts of participants affected, but they do not establish causation, and death counts are not reported in the registry record.

Overall, the record supports a careful account of the posted treatment means and simple comparison estimates. It does not resolve the sponsor’s adjusted crossover analysis, the clinical meaning of the estimated differences, the handling of all missing period data, or the broader applicability of the findings. Those limits should remain part of any interpretation.

17. Why This Trial Matters Statistically

This trial illustrates why the design behind a comparison matters as much as the values in a results listing. In a crossover study, participants receive multiple treatments, so observations across treatments are linked within individuals. An analysis that uses this structure may differ from a simple comparison of treatment means and standard deviations. The registry describes a patient-and-period model for the primary endpoint, but does not report its numerical results. That gap makes it especially important to distinguish descriptive recalculations from the sponsor’s intended model-based analysis.

The record also shows how precision can change across outcomes. The primary EET comparison for Symbicort has an interval above zero under the simple calculation, whereas the formoterol interval includes zero. Other endpoint summaries have their own scales and uncertainty. A single unadjusted p-value cannot convey the design assumptions, the range of plausible effects, or whether an effect is meaningful to patients.

Multiplicity is another key statistical issue. Several treatment contrasts and many outcomes are listed, yet the registry record does not report a strategy for controlling or interpreting multiple tests. This is a common reason to avoid treating each unadjusted secondary result as a separate confirmation.

Finally, planning illustrations based on observed effects are not a record of the trial’s original design justification. They show how assumed effect size and desired power influence sample-size requirements under stated simplifying assumptions. They cannot explain why enrollment was set at its observed level or substitute for the original protocol’s rationale, which is not reported in the registry record.

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.

Several limitations are specific to interpreting this study’s posted results. First, it used a crossover design, but the numerical sponsor estimates from the described patient-and-period model are not reported. The available simple contrasts use treatment-level summaries and do not capture within-person covariance. Their uncertainty may not match the uncertainty from the crossover model.

Second, the primary endpoint description excludes patients with only one EET measurement from the sponsor’s model, which required data from at least two periods. The record does not report the number excluded for this reason, the pattern of missing treatment-period values, or how missing data were handled in other analyses. Treatment-level participant counts cannot establish how many participants contributed complete measurements across periods.

Third, the registry record does not provide a complete statistical analysis plan. The original sample-size justification, interim analyses, analysis-population definitions, multiplicity procedures, and full crossover model specification are not reported. The record also does not explain whether sequence or carryover effects were considered. These absences limit assessment of whether the posted comparisons match the planned primary analysis.

Fourth, the recalculated results are unadjusted and based on posted summary statistics. Multiple outcomes and comparisons make isolated p-values less persuasive when no multiplicity strategy is described. The record does not state a threshold for a clinically meaningful EET difference, so statistical uncertainty cannot be translated into a claim about clinical importance.

Finally, safety information is limited to affected-participant counts and listed event terms. Death counts and detailed timing or attribution are not reported in the registry record. The available information supports a descriptive account, not a causal comparison of adverse-event risk.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Evaluation of Efficacy on Exercise Tolerance of Symbicort (Budesonide/Formoterol) Compared to Placebo and Oxis in Patients With Severe COPD — NCT00489853.
• Registry record last updated 2012-08-30; status last verified 2012-07.
• Results first posted 2012-08-30.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

This completed phase 4 randomized, quadruple-masked crossover study enrolled 137 patients with severe COPD and compared Symbicort, formoterol, and placebo. The primary outcome was cycle-ergometry EET at 75% of peak work capacity, measured 1 hour after dosing at the end of each 1-week treatment period.

Posted means were 529.0 seconds for Symbicort, 441.0 seconds for formoterol, and 406.0 seconds for placebo. Simple unadjusted comparisons show a mean difference of 123.0 seconds for Symbicort versus placebo and 35.0 seconds for formoterol versus placebo. These recalculations are not the sponsor’s crossover-model results, which are not reported in the registry record.

The registry lists numerous secondary outcomes and provides summaries for several, along with adverse-event counts. The analysis plan, multiplicity handling, missing-data details, original sample-size rationale, and death counts are not reported in the registry record. Interpretation should distinguish the posted descriptive estimates from conclusions requiring those missing details.