Step-up Yellow Zone Inhaled Corticosteroids to Prevent Exacerbations: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Step-up Yellow Zone Inhaled Corticosteroids to Prevent Exacerbations (NCT02066129), a randomized phase 3 study. The primary outcome is Asthma Exacerbations.

2. Clinical Question

The question is specific to a dose step-up triggered by yellow-zone symptoms in children already receiving low-dose ICS. It does not ask whether inhaled corticosteroids prevent asthma in general, or whether the regimens have the same effects outside the treatment period. The registry record does not report additional questions about subgroups or longer-term outcomes.

3. Trial Design

The registry identifies NCT02066129 as a completed phase 3, randomized, quadruple-masked, parallel-group trial. The sponsor was Milton S. Hershey Medical Center. Enrollment was 254. The registry records a start date of 2014-07 and primary completion on 2017-04-21.

Participants were assigned to one of two fluticasone regimens. The Fluticasone 44 mcg group used 2 puffs twice daily for 7 days when yellow-zone symptoms began. The Fluticasone 220 mcg group used the same schedule and timing. The comparison therefore concerns the registered dose strengths within this symptom-triggered regimen; it is not a comparison of different treatment durations or symptom triggers.

The posted primary outcome is the rate of severe asthma exacerbations treated with oral corticosteroids over the 48 week treatment period. Results are reported as least-squares means with 95% confidence intervals. Each arm has a reported sample size of 127. The registry also lists secondary outcomes concerning yellow-zone asthma symptoms, yellow-zone albuterol use, unscheduled emergency department or urgent care visits for asthma, and participants hospitalized for asthma.

Quadruple masking indicates the registry’s masking classification, but the identities of the masked parties and the practical masking procedures are not reported in the registry record. Details of the randomization sequence, allocation concealment, trial sites, and adherence assessment are also not reported in the registry record. The design label alone does not establish how these 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.

Overall Study

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 Asthma Exacerbations, measured over end of 48 week treatment period.

The primary endpoint is the rate of severe asthma exacerbations treated with oral corticosteroids during the 48 week treatment period. The registry expresses the outcome in exacerbations per year and reports a least-squares mean for each arm with a 95% confidence interval. The outcome is intended to capture event frequency over time, not only the proportion of participants who had at least one event.

As a general statistical point, a rate can be useful when an outcome may occur repeatedly and when the observation period is part of the interpretation. It connects the number of events with the time during which those events were observed. A rate does not, by itself, describe how events were distributed among participants: the same group rate could arise from different patterns of recurrence across individuals.

Using severe exacerbations treated with oral corticosteroids makes the endpoint relevant to the trial’s stated objective. At the same time, interpretation depends on how an exacerbation was defined, how events were identified, and how follow-up time was handled. Those operational details are not reported in the registry record beyond the endpoint description and treatment-period timeframe. The posted estimates should therefore be read as the registry’s reported rate summaries, not as a complete account of outcome ascertainment or the analysis procedure.

7. Results Posted in the Registry

• Fluticasone 220 mcg: 0.48 versus 0.37 (exacerbations per year) on control; rate ratio 1.30 (95% CI 0.75–2.24, derived from the posted confidence limits); p ≈ 0.349.

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.

Number of Participants Hospitalized for Asthma

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Fluticasone 220 mcg: 3.1% (4/127) versus 0.0% (0/127) on control; risk difference 3.1 percentage points (95% CI 0.1 to 6.2); unadjusted two-proportion z-test p = 0.044.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Fluticasone 220 mcg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes spanning yellow-zone asthma symptoms, albuterol use, unscheduled emergency department or urgent care visits for asthma, and hospitalization for asthma. These outcomes cover symptom experience, rescue medication use, acute health care, and a more severe consequence. They are related to the primary question, but they are not interchangeable with the primary rate of exacerbations treated with oral corticosteroids.

Results are posted for hospitalization, while outcome-specific results for the other listed secondary measures are not reported in the registry record. This limits how fully the secondary evidence can be compared with the primary result. A secondary measure may capture a different aspect of asthma burden, and a pattern across outcomes should not be inferred from outcomes whose estimates are not reported.

The hospitalization comparison is an unadjusted secondary result. It should be interpreted as a separate outcome rather than as a confirmation or contradiction of the primary rate comparison. The primary endpoint and hospitalization measure differ in their definition and statistical scale, so an apparent difference in one does not automatically explain the other.

As a general statistical concern, examining multiple outcomes creates more opportunities for apparently noteworthy findings to arise by chance. The registry record does not report whether a multiplicity adjustment or a hierarchy for secondary outcomes was planned. Consequently, unadjusted secondary results generally carry less weight than a prespecified primary analysis, particularly when the analysis plan and completeness of results are unclear. The secondary outcomes can add context, but they do not replace the primary result or resolve its uncertainty.

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

• Yellow Zone Asthma Symptoms
• Yellow Zone Albuterol Use
• Unscheduled Emergency Department (ED) or Urgent Care Visits for Asthma
• Number of Participants Hospitalized for Asthma

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports the primary outcome as a least-squares mean rate with a 95% confidence interval. This combines a group-level estimate with an interval describing statistical uncertainty. The registry record does not provide enough information to reconstruct the full model that produced the least-squares means, including any covariates or model diagnostics.

What does a rate represent?

As a general statistical concept, an event rate relates the number of observed events to time at risk or exposure. This is useful for outcomes that can recur, because it retains information about repeated events instead of reducing everyone to a yes-or-no indicator. The registry’s unit is exacerbations per year, and its primary timeframe is the end of the 48 week treatment period. The exact method used to account for differing observation time is not reported in the registry record.

Rates are not the same as risks. Risk generally concerns whether an event occurred over a specified period, while a rate concerns event occurrence relative to time. Nor does a group-level rate reveal whether events were concentrated in a small number of participants or spread across the group. Participant-level event histories would be needed to describe that pattern.

What does a confidence interval communicate?

As a general explanation, a confidence interval gives a range of estimates compatible with the data and the method used, under the assumptions of that method. It is not a range containing a fixed proportion of individual participants’ outcomes, and it is not a guarantee that the true effect lies within the interval. A wider interval indicates less precision than a narrower interval on the same scale.

The arm-specific intervals describe uncertainty around each reported rate. The comparative rate ratio is a separate summary: it expresses the relative rates between the two arms. The posted rate-ratio estimate is 1.297. Its confidence interval spans the no-rate-difference value, so the comparison remains compatible with equal rates as well as with effects in either direction. The exact lower endpoint is not repeated in this explanation because it is reported with more than 3 decimal places.

How should the p value be read?

The unadjusted p value is 0.349. In general, a p value describes how unusual data at least as discrepant as those observed would be under a specified statistical model when its null hypothesis holds. It does not measure the size or clinical importance of an effect, and it does not give the probability that the null hypothesis is true. The registry does not report a full analysis plan, so the assumptions and decision rules beyond the posted statistic are not described in the registry record.

Why can rate data need special care?

As a general matter, count outcomes may vary more than a simple model assumes. Over-dispersion means the observed variability exceeds the model’s expected variability; if not handled appropriately, standard errors and intervals can be too optimistic. Conversely, a model that does not fit the event process can misstate uncertainty. The registry identifies the primary result as a rate but does not report enough methodological detail to determine how over-dispersion, recurrent events, or unequal follow-up were evaluated.

The posted comparison also includes a recalculated, unadjusted rate ratio and p value. These are not a replacement for a sponsor analysis. The discrepancy flag is false, so no disagreement with a sponsor analysis is identified in the registry information. The registry record does not provide details that would allow an independent reconstruction of the model-based primary estimates from participant-level data.

Finally, interpretation should distinguish estimation from decision-making. The estimated rates and interval describe the outcome and its uncertainty; they do not establish a treatment recommendation. The results concern the registered population, regimens, endpoint definition, and treatment period. General statistical concepts can clarify what the estimates mean, but cannot fill in trial methods that are not reported in the registry record.

11. Confidence Intervals and Precision

The arm-specific estimates are 0.37 exacerbations per year for Fluticasone 44 mcg, with a 95% confidence interval from 0.25 to 0.55, and 0.48 for Fluticasone 220 mcg, with a 95% confidence interval from 0.33 to 0.7. These intervals express uncertainty around the reported rates. They overlap, but overlap between separate arm intervals is not, by itself, a formal test of the difference between arms.

The registry also reports a rate ratio of 1.297. Its interval includes the value representing equal rates, which indicates that the comparative estimate is not precise enough to rule out no rate difference. The interval also allows effects on either side of that benchmark. This is why the point estimate should not be read alone as establishing a difference.

In general, confidence intervals convey precision, not importance. A narrow interval can still concern an outcome of limited relevance, while a broad interval can include effects that would matter in different directions. The registry does not report a prespecified threshold for a clinically important difference, so the interval cannot be judged against such a threshold from the record.

The reported sample size is 127 in each arm. That context does not remove the uncertainty in the rate estimates, and the registry record does not report a trial-specific precision target. The interval and the comparison’s uncertainty are therefore central to interpreting the posted result.

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 illustrations based on the observed effect, not a report of the trial’s original design calculation. They assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

For the full observed effect, the planning illustration gives 603 participants per arm for 80% power and 807 participants per arm for 90% power. For planning for 75% of the observed effect, it gives 1,103 participants per arm for 80% power and 1,477 participants per arm for 90% power. For planning for 50% of the observed effect, it gives 2,557 participants per arm for 80% power and 3,424 participants per arm for 90% power. These are participant counts per arm, not total event counts.

In plain terms, the 80% column gives the planned number of participants per arm under which the calculation would have an 80% chance of detecting the assumed effect, if the assumptions and model held. The 90% column applies the higher target probability, also under those assumptions. These planning values are not observed power.

The pattern follows a general principle: smaller effects are harder to distinguish from random variation, so the calculation requires more participants. The figures use an effect derived from the observed comparison, which is uncertain; they should be treated as planning scenarios rather than as evidence that a future study will achieve a particular result.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control rate λ₀ = 0.3700; treatment rate λ₁ = 0.4800 events per patient-year; follow-up T = 0.92 years.
2. n = (1.96 + 0.842)² × (1/0.3700 + 1/0.4800) / (0.92 × [ln(1.297)]²) = 602.8, rounded up to 603 participants per arm for 80% power.

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

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
lambda0 <- 0.37                      # control rate, events per patient-year
lambda1 <- 0.48                      # treatment rate
tt      <- 0.919892679187428                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^2), 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(2066129)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 603 (80% power), 807 (90% power)
 75% of observed effect: n per arm = 1,103 (80% power), 1,477 (90% power)
 50% of observed effect: n per arm = 2,557 (80% power), 3,424 (90% power)
Simulated power, Poisson counts, n = 603 per arm: 0.800
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.638

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

14. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple secondary outcomes alongside the primary endpoint. The record does not report a multiplicity strategy, such as a hierarchy among outcomes or an adjustment to account for testing several questions. Without that information, unadjusted secondary comparisons should be treated as exploratory evidence rather than as independent confirmation of a primary finding. The posted secondary analyses should not be assumed to have been prespecified in a particular order.

Missing-data procedures are not reported in the registry record. The record does not explain how participants with incomplete follow-up, missing outcome measurements, or incomplete event reporting were handled. It also does not identify the analysis population, such as whether the primary analysis followed assigned groups regardless of adherence. Those details matter because different choices can change the population represented by an estimate and the uncertainty around it.

The registry’s analysis listing does not describe the full statistical plan. Model covariates, diagnostics, handling of recurrent events, and approaches to departures from model assumptions are not reported in the registry record. An interim analysis plan and stopping rules are also not reported in the registry record. Their absence from the record should not be taken as evidence that a particular procedure was or was not used.

These gaps constrain the interpretation of the posted results. The estimates and confidence intervals remain descriptive of the registry’s reported analysis, but readers cannot use the record alone to verify all analysis decisions or assess sensitivity to missing data and alternative models. A protocol or statistical analysis plan would be needed to clarify these matters; neither is described in the registry record.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: asthma exacerbation (3.1%), hypertrophy tonsils/adenoids (0.8%).

The registry reports serious adverse events for 127 participants at risk in each arm. Serious adverse events affected 1 participant in the Fluticasone 44 mcg group and 4 participants in the Fluticasone 220 mcg group. The registry records 0 deaths in each group. These are counts as posted; they do not establish that the regimens caused the events.

The listed serious adverse-event terms include Asthma Exacerbation at 3.1% and Hypertrophy Tonsils/Adenoids at 0.8%. The registry record does not make the arm-specific allocation of these listed term percentages clear, so they should not be assigned to a particular arm on the basis of this information alone.

Other adverse events affected 115 participants in the Fluticasone 44 mcg group and 111 in the Fluticasone 220 mcg group. These figures are distinct from the serious-event counts and should not be combined with them. Adverse-event summaries describe reported events during the study; without further detail on event definitions, timing, severity, and attribution, they do not by themselves establish a causal safety comparison.

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

The posted primary estimates show a higher point estimate for the Fluticasone 220 mcg arm than for the Fluticasone 44 mcg arm, but the comparative uncertainty includes equal rates. The unadjusted p value is 0.349. Taken together, the registry results do not establish a clear difference between the two registered regimens on the primary endpoint. The interval remains important: it indicates that the data are compatible with a range of comparative effects.

This result does not show that the regimens are equivalent. Demonstrating equivalence or noninferiority requires an appropriate prespecified margin and analysis; those are not reported in the registry record. Nor does a nonsuggestive p value prove that there is no effect. The finding is uncertainty about the comparison, not proof of sameness.

The result also does not establish what would happen outside the registered setting. It concerns children receiving low-dose ICS, the two symptom-triggered fluticasone regimens, the specified primary outcome, and the 48 week treatment period. Details needed to characterize the population more fully are not reported in the registry record. The findings should not be generalized automatically to other populations, regimens, or follow-up periods.

Secondary outcomes address other aspects of asthma and care, but their results and analysis plans are not complete enough in the registry record to settle the primary question. Unadjusted findings on a secondary endpoint cannot, by themselves, override the primary comparison. Similarly, adverse-event counts describe events reported in the groups but do not establish causation.

In general, a trial estimate is evidence about a defined comparison, not a direct instruction for individual care. The registry record supports describing the reported rates, the comparative estimate, and their uncertainty. It does not supply all the protocol and analysis details needed to resolve every potential source of bias or to make broader claims.

17. Why This Trial Matters Statistically

This trial illustrates why the choice of outcome scale matters. The primary endpoint is a rate of recurrent severe exacerbations treated with oral corticosteroids, rather than a simple count of participants with any exacerbation. That distinction affects both the clinical question and the statistical analysis: rates address how frequently events occur relative to time, while a participant count addresses whether an event occurred.

The example also shows why an estimate should be read with its uncertainty. The two arm-level point estimates are not the whole result; their confidence intervals and the comparative interval indicate that plausible effects remain on either side of equal rates. A single point estimate can appear definitive when the available precision does not support that conclusion.

Planning calculations based on an observed effect are another useful teaching case. They show how the required participant count depends on the effect a future study aims to detect and the desired power. Because the observed effect is itself uncertain, such calculations are illustrations, not evidence of the power actually achieved by the completed trial or a substitute for the original design rationale.

Finally, the record demonstrates the importance of transparent analysis reporting. Information about missing data, analysis populations, multiplicity, and model assumptions is needed to assess how robust estimates may be. When these details are absent, interpretation can still describe the posted results, but should be appropriately bounded.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The registry record does not report detailed eligibility criteria, participant age ranges, or other baseline characteristics. This makes it difficult to judge how closely the enrolled children match any particular clinical population. The record identifies the sponsor but does not report trial-site details, so the setting and geographic breadth cannot be assessed from this information.

The primary endpoint is described as severe asthma exacerbations treated with oral corticosteroids, but the record does not give a detailed operational definition or explain how events were verified. It also does not describe the method for handling repeat events or differences in follow-up time. These omissions matter for interpreting a rate endpoint.

The record does not report the analysis population, missing-data approach, covariate adjustment, or full model specification. It also does not describe multiplicity control for the secondary outcomes. The posted unadjusted secondary findings should therefore be interpreted cautiously, and the primary result cannot be independently reconstructed from the registry record alone.

The treatment period is 48 weeks; outcomes beyond that period are not described. Several listed secondary outcomes do not have outcome-specific results in the registry record. The record also does not report adherence or whether participants followed the assigned regimen as intended. These limits narrow what can be concluded about the completeness and scope of the posted findings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Step-up Yellow Zone Inhaled Corticosteroids to Prevent Exacerbations — NCT02066129.
• Registry record last updated 2018-07-11; status last verified 2018-06.
• Results first posted 2018-07-11.
• 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

NCT02066129 is a completed, randomized, quadruple-masked, parallel-group phase 3 trial sponsored by Milton S. Hershey Medical Center. It enrolled 254 children with asthma receiving low-dose ICS and compared two fluticasone strengths, both administered for 7 days at the onset of yellow-zone symptoms.

The primary outcome was the rate of severe asthma exacerbations treated with oral corticosteroids during the 48 week treatment period. The reported arm-level rates were 0.37 and 0.48 exacerbations per year, with a rate ratio of 1.297 and an unadjusted p value of 0.349. The comparison remains uncertain and does not establish a clear difference.

The registry lists secondary outcomes and adverse-event summaries, but does not report several details of the statistical plan, missing-data handling, or analysis populations. Those omissions limit assessment of robustness and scope.