Use of Dexamethasone in Pediatric Asthma Exacerbations: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Use of Dexamethasone in Pediatric Asthma Exacerbations (NCT02192827), a randomized phase 3 study. The primary outcome is Number of Participants Returning to Care Following Discharge From the Emergency Department.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, parallel-group trial with no masking, according to the registry record. The sponsor was the University at Buffalo. The registry lists the study as starting in 2015-04, with primary completion in 2018-03, and its status is completed. The condition listed is asthma.

The registry describes a comparison of single-dose and two-dose dexamethasone for mild to moderate pediatric asthma exacerbations in the emergency department. In the single-dose group, dexamethasone sodium phosphate was given orally once in the emergency department. The two-dose group received that same initial dose, followed by a second dose at home that was prescribed from the emergency department. The stated dose was 0.6 mg/kg. No masking was used, so the study is recorded as open-label in the sense that masking was absent; the registry does not report further details about who knew each participant’s assignment.

The registry reports 318 enrolled participants. For the posted primary outcome, each arm has 116 participants in its denominator. The record does not explain the relationship between the overall enrollment figure and those outcome denominators, so no reason for the difference can be inferred from these figures alone. The available record also does not report the original sample-size justification, allocation-concealment procedures, eligibility criteria beyond the summary description, or the trial’s planned statistical analysis in detail.

The primary outcome was the number of participants returning to care following emergency-department discharge, measured over 5 days. A secondary outcome listed is reported days until symptom resolution over 5 days. The registry reports no analyses in its analyses listing. The results presented for the outcomes therefore need to be read as posted arm-level outcome data and unadjusted comparisons, rather than as evidence that a particular prespecified or adjusted analysis was carried out.

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: Excluded 10 Patients: Previously enrolled into the study: 2 Admitted to the PICU (pediatric intensive care unit): 5 Required IV steroids in the Emergency Dept: 1 Steroid use within the last 2 weeks: 1 Excessive vomiting in the Emergency Dept: 1

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 Number of Participants Returning to Care Following Discharge From the Emergency Department, measured over 5 days.

The primary endpoint counts participants who had any unscheduled visit to an emergency room, urgent care, or primary care physician after discharge from the emergency department. The assessment window was 5 days. Each participant is counted as having the event or not having the event according to the investigators’ definition; the measure is a participant count, not a count of the total number of visits. A participant with more than one qualifying visit would still be represented as a participant with an event in this endpoint description.

This kind of endpoint is used to describe subsequent use of health care after the initial emergency-department encounter. It can summarize whether participants returned for additional care during a specified follow-up period. It does not by itself identify why a return visit occurred, how severe the underlying symptoms were, or whether the visit was driven by clinical need, access, or other factors. Those details are not reported in the endpoint description.

The registry reports 14 participants with the event in the single-dose group and 12 in the two-dose group, with 116 participants in each posted outcome denominator. The comparison is therefore about recorded return-to-care events within the stated follow-up window. It should not be interpreted as a complete measure of all aspects of asthma symptoms or recovery.

7. Results Posted in the Registry

• Two Dose Dexamethasone: 10.3% (12/116) versus 12.1% (14/116) on control; risk difference -1.7 percentage points (95% CI -9.8 to 6.4), risk ratio 0.86 (0.41–1.77); unadjusted two-proportion z-test p = 0.677.

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.

Reported Number of Days Until Symptom Resolution

• 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:
  • Two Dose Dexamethasone: mean 2.50 versus 2.40 on control; difference 0.10 (95% CI -0.79 to 0.99), standardized effect d = 0.03; z-test p = 0.825.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Two Dose Dexamethasone and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists reported days until symptom resolution as a secondary outcome. Its overall pattern is close between the groups, with a small posted difference in the means and a confidence interval that spans values on both sides of zero. This does not offer a clear separation between the groups on that measure. The primary outcome also has a small difference in the posted event counts and an interval that includes zero. Considered together, the outcomes do not show a consistent, precise signal of a difference across the measures reported.

The secondary measure relates to the primary result by addressing a different aspect of the post-treatment course. Return to care records whether a participant had an unscheduled visit, whereas days until symptom resolution summarizes reported time to resolution. Similar patterns across different outcomes can be useful context, but one endpoint does not validate another. Neither outcome alone establishes equivalence, and the registry does not report a prespecified relationship or hierarchy between them.

Unadjusted secondary results generally carry less weight than a clearly specified primary analysis when multiple outcomes or analyses are considered. General statistical explanation: testing many outcomes increases the chance that at least one result may look unusual by chance if each is interpreted without accounting for the number of tests. A multiplicity strategy can address that issue, but no such strategy is reported in the registry record. The record also lists no reported analyses, so it is not possible to determine whether the secondary comparison was prespecified or how it fits into the investigators’ complete analysis plan.

Accordingly, the secondary result is best treated as supportive descriptive information rather than independent confirmation. It should be interpreted alongside its estimate, uncertainty, and reporting limitations, without elevating an unadjusted p-value into a standalone conclusion. The registry does not report additional detail about missing observations or outcome-assessment procedures that would clarify the robustness of the secondary analysis.

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

• Reported Number of Days Until Symptom Resolution

9. Statistical Interpretation

10. Statistical Methods Explained

For the primary outcome, the endpoint is binary at the participant level: a participant either had at least one qualifying unscheduled return visit during the 5-day window or did not. The posted summaries give the number of participants with an event and the number in each group. A risk difference expresses the difference between the two groups’ event proportions, with the sign depending on which group is subtracted from which. The posted estimate is defined for the two-dose group relative to the single-dose group. A negative estimate therefore points toward fewer recorded events in the two-dose group in this coding, while a positive estimate points in the opposite direction.

A confidence interval around a risk difference describes a range of values reasonably compatible with the observed data under the method used to calculate the interval. It conveys uncertainty about the estimated difference. If the interval includes zero, the data do not distinguish the estimate from no difference at the conventional level associated with that interval method. That does not prove that the true difference is zero. The interval also helps show whether the data exclude effects that might matter; interpretation requires a context-specific threshold, which is not reported for this outcome.

The p-value is an unadjusted test result. In general, a p-value measures how unusual the data, or more extreme data, would be under a specified null model and assumptions. It is not an effect-size measure, and it does not tell whether a result is clinically important. The posted p-value is 0.677. The registry does not report a detailed statistical plan or say whether this test was prespecified, adjusted for other variables, or part of a sequence of analyses. It should therefore be read as the unadjusted comparison shown in the posted results.

Other common ways to express a binary comparison include a risk ratio and an odds ratio. A risk ratio compares the event risks between groups, while an odds ratio compares event odds. These measures answer related but distinct questions and are not interchangeable with a risk difference. The posted result includes these relative measures, but their intervals are broad; the main interpretation relies on the primary risk-difference comparison and its uncertainty. No adjusted estimate is reported.

What does the symptom-resolution comparison measure?

The secondary outcome is a mean: the reported average number of days until symptom resolution during the stated 5-day timeframe. The registry gives a mean and standard deviation for each group. The mean difference is the two-dose group’s mean minus the single-dose group’s mean, as reflected by the posted estimate of 0.1 days. In general, a mean difference summarizes the average separation between groups, while the standard deviation describes variation among participant-level observations within a group. A standard deviation is not a confidence interval for the mean and does not say how certain the group mean is.

The confidence interval for the mean difference runs from -0.788 to 0.988, and the unadjusted p-value is 0.825. Because the interval includes zero and spans values in both directions, it does not identify a clear difference in average reported resolution time. The interval is the more informative expression of uncertainty than the p-value alone, though its clinical interpretation would require a threshold for meaningful change. No such threshold is reported.

Why does over-dispersion matter?

General statistical explanation: for a count outcome, a simple model may assume that variability is determined by the mean. If actual variability is greater than that assumption allows, the data are over-dispersed. Ignoring over-dispersion can make uncertainty appear too small and can make statistical tests look more decisive than warranted. The primary endpoint is posted as the number of participants with an event, which is a binary outcome rather than a repeated-visit count. The registry does not report a model for repeated visits or an over-dispersion assessment. The distinction matters because this endpoint counts participants with any return, not the total number of visits.

What can the registry’s analysis record establish?

The registry lists no reported analyses. Posted summary comparisons nevertheless include unadjusted estimates, intervals, and p-values. The record does not explain the statistical method used to produce each interval or test, whether covariates were considered, how missing data were handled, or whether the reported comparisons correspond to the original analysis plan. These details are not reported in the registry record, so the estimates should not be described as adjusted or as confirming a particular analysis strategy.

General statistical explanation: randomization can support a fair comparison by balancing, on average, factors that influence outcomes, but the strength of that interpretation also depends on implementation, follow-up, and analysis. Randomization does not automatically prevent missing-outcome bias, guarantee concealment, or make a small number of events precise. The registry identifies the trial as randomized but does not report enough information to assess all of these features.

11. Confidence Intervals and Precision

Precision concerns how tightly the data locate an effect estimate. For the primary outcome, the risk-difference interval extends from -0.098 to 0.064 in the posted comparison. It crosses zero, which means the interval includes both a possible reduction and a possible increase in the event risk under the stated contrast. The interval is wide relative to the point estimate, so the direction and size of the underlying difference remain uncertain. The event counts are modest, and the outcome denominators are 116 in each arm; the interval communicates that uncertainty more fully than the point estimate alone.

The p-value of 0.677 is consistent with the interval not identifying a clear difference, but it does not measure precision by itself. A p-value can be large when an estimate is close to zero, when the data are imprecise, or both. The confidence interval shows the range of effects compatible with the data under its method and assumptions. Since a clinically acceptable difference is not reported, the interval cannot be used to establish that any remaining difference is unimportant.

For symptom-resolution time, the mean-difference interval is -0.788 to 0.988 days. It includes zero and allows differences in either direction. The posted means are close, but closeness of point estimates is not the same as precision. The interval gives a broader account of uncertainty around the difference. No equivalence margin or minimum clinically important difference is reported for this outcome.

In general, confidence intervals quantify sampling uncertainty under a statistical method; they do not account automatically for bias, missing data, outcome misclassification, or departures from the method’s assumptions. Since the registry does not report the detailed analysis plan or missing-data handling, the intervals should be understood as posted statistical summaries rather than a complete accounting of every source of uncertainty.

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 effects, not the trial’s original design assumptions. The registry record does not report the original sample-size justification. The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses a stated fraction of the observed effect as the effect to detect.

For the primary binary outcome, the planning figures are participants per arm. For example, planning for 100% of the observed effect gives 5,254 participants per arm for 80% power and 7,033 participants per arm for 90% power. Planning for 75% of the observed effect gives 9,498 participants per arm for 80% power and 12,714 participants per arm for 90% power. Planning for 50% of the observed effect gives 21,721 participants per arm for 80% power and 29,078 participants per arm for 90% power.

In plain terms, 80% power describes a design that would have an 80% chance of detecting the specified effect under the planning assumptions if that effect were present. The 90% column describes the corresponding chance as 90%. The higher-power target requires more participants for the same effect. Smaller effects require more participants because they are harder to distinguish from random variation.

These figures are not observed power. They are forward-looking planning illustrations calculated from the observed effect, and the observed effect may itself be uncertain. They do not establish the power of the completed trial or explain how its original enrollment target was chosen. The sample-size curve should be read as illustrating how the required participants per arm changes with the effect size under the stated assumptions, not as a guarantee of a future study’s results.

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 = 0.121; treatment proportion p₁ = 0.103; average p̄ = 0.112.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4461 = 0.8744.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4459 = 0.3753.
4. n = (0.8744 + 0.3753)² / (-0.0172)² = 5,253.6, rounded up to 5,254 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 <- 0.120689655172414                          # control proportion
p1 <- 0.103448275862069                          # 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(2192827)
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 = 5,254 (80% power), 7,033 (90% power)
 75% of observed effect: n per arm = 9,498 (80% power), 12,714 (90% power)
 50% of observed effect: n per arm = 21,721 (80% power), 29,078 (90% power)
power.prop.test: 5253.6 
Simulated power at n = 5,254 per arm: 0.804 (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 record does not report a multiplicity plan. It does not state whether the primary outcome was tested in a formal hierarchy with the secondary outcome, whether any adjustment was made for multiple comparisons, or whether additional planned analyses were conducted. Because the record lists one secondary outcome and no reported analyses, the status of any broader outcome-testing strategy is unclear. Unadjusted secondary results should therefore be interpreted cautiously: when several outcomes or tests are examined, chance alone can make one result appear more notable than it would be under a plan that accounts for multiple testing.

The record also does not report how missing outcome data were handled. The posted primary outcome denominators are 116 per arm, while overall enrollment is listed as 318. These figures do not explain whether participants lacked outcome data, were excluded from an analysis, or entered the posted results under a different accounting. No missingness pattern or imputation method is reported. It is therefore not possible to assess from the registry record whether missing outcomes could have affected the comparisons.

The analysis population is not reported. For example, the record does not identify whether the posted summaries use all randomized participants, only participants with available outcome data, or another population definition. The fact that the study was randomized does not by itself establish which participants were included in each reported analysis. Nor does the record describe deviations from assigned treatment or how they were handled analytically.

These omissions do not show that a particular problem occurred; they limit what can be concluded about the analysis. No protocol details, statistical analysis plan, prespecified handling of missing data, or multiplicity adjustments are reported in the registry record. The posted comparisons can be described as unadjusted, but further claims about prespecification, intention-to-treat analysis, or correction for multiple testing would go beyond the information reported.

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 non-serious adverse event terms

The serious adverse event figures report zero affected participants among 116 at risk in the single-dose group and zero among 116 at risk in the two-dose group. No deaths are reported in either group. These are counts recorded in the registry, not evidence that no serious events could occur or that the groups have identical safety profiles. The figures describe the posted observations and their stated at-risk denominators.

The registry also reports other adverse events in the groups: 20 in the single-dose group and 10 in the two-dose group, with 116 at risk in each. These counts are separate from the serious adverse event figures. The record does not provide the event terms in the information reported for this comparison, so the types, severity, timing, and relationship to treatment cannot be characterized. The counts alone do not establish a causal difference between groups.

In general, safety interpretation depends on what events were defined and collected, how long participants were followed, and how complete reporting was. The available record gives the counts but does not report enough detail to assess those features. The figures should therefore be read narrowly as registry-reported adverse event summaries, not as a comprehensive safety comparison.

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

The posted results describe a randomized comparison of one versus two doses of dexamethasone for mild to moderate pediatric asthma exacerbations. For the primary endpoint, the registry records 14 participants returning for unscheduled care in the single-dose group and 12 in the two-dose group, with 116 participants in each reported denominator. The unadjusted p-value is 0.677, and the interval for the risk difference crosses zero. The data do not identify a clear difference in return-to-care events, but they also do not establish that the regimens are equivalent.

The secondary symptom-resolution result is similarly uncertain: the reported means are 2.4 days and 2.5 days, and the confidence interval for their difference includes zero. This is descriptive evidence about the reported endpoint, not proof that the underlying averages are the same. An absence of a clear statistical difference is not the same as evidence that any difference is small enough to be unimportant. Such a conclusion would require an agreed margin for an acceptable difference and an analysis designed to assess it; neither is reported in the registry record.

The registry’s title uses language of equal effectiveness, but the posted comparison should be interpreted according to its design and analysis details as reported. The registry does not report an equivalence margin, a detailed statistical plan, missing-data handling, or the analysis population. The posted intervals therefore describe uncertainty in the reported comparisons, while some important sources of uncertainty cannot be assessed from the record.

These findings should not be used as medical advice or as a recommendation about dosing. They concern the outcomes and follow-up period specified in the registry, especially unscheduled return to care within 5 days. They do not address every possible outcome, longer-term experience, or all children with asthma. The results support a cautious statistical reading: the observed group summaries are close, but the available information does not justify a claim of identical effects or a broad conclusion beyond the reported outcomes.

17. Why This Trial Matters Statistically

This trial illustrates why a small difference between observed group summaries does not settle the question of whether two regimens have the same effect. The primary event counts are close, but the confidence interval extends in both directions around no difference. Statistical interpretation depends not only on the point estimate but also on how much uncertainty surrounds it and on what differences would matter in practice.

It also highlights the distinction between testing for a difference and testing for equivalence. A conventional unadjusted comparison asks whether the data provide evidence against a no-difference model. Equivalence asks whether the data are sufficiently precise to exclude differences larger than a prespecified acceptable margin. The registry record does not report such a margin or an equivalence analysis, so the title’s wording cannot be established by the posted p-value alone.

The outcome itself matters. A return-to-care endpoint captures any qualifying unscheduled visit during a specified follow-up window, not the total burden of visits or the full course of symptoms. The secondary symptom-resolution measure offers a different perspective, but its unadjusted result does not replace the primary endpoint or remove uncertainty about either measure.

Finally, reporting detail is part of statistical interpretation. The registry provides randomized design information and posted outcome summaries, but not the original sample-size justification, analysis population, missing-data method, or multiplicity strategy. Recognizing what is and is not documented helps distinguish observed results from stronger claims that would require additional design and analysis information.

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 trial-specific limitations constrain interpretation. The study is recorded as having no masking. The registry does not explain whether participants, clinicians, or outcome assessors knew assignments, or how that may have affected treatment delivery or reporting. The primary endpoint involves unscheduled care, an outcome that depends on a participant having a qualifying visit; details about how those visits were verified or classified are not reported.

The registry lists 318 participants enrolled overall, whereas the posted primary outcome has 116 participants in each group. The record does not explain this difference. It does not report participant flow, the number with missing outcomes, exclusions from the outcome summaries, or the analysis population. Consequently, the outcome denominators cannot be assumed to represent all randomized participants, and the potential effects of missingness cannot be assessed.

The original sample-size justification and detailed statistical analysis plan are not reported. Neither an equivalence margin nor a multiplicity strategy is stated. The posted comparisons are unadjusted, and the registry lists no reported analyses. It is not possible to determine whether the reported comparisons follow prespecified methods or whether other analyses were planned.

The primary follow-up window is 5 days, so the endpoint describes return to care over that period rather than longer-term outcomes. The registry also gives limited detail about the secondary outcome’s measurement and reports no additional context for the adverse event terms. The available information supports describing the posted results, but not a comprehensive assessment of trial conduct, endpoint ascertainment, or all relevant outcomes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Use of Dexamethasone in Pediatric Asthma Exacerbations — NCT02192827.
• Registry record last updated 2023-03-30; status last verified 2023-03.
• Results first posted 2023-03-30.
• 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

The registry record describes NCT02192827, a completed Phase 3 randomized, parallel-group trial sponsored by the University at Buffalo. The study compared one dose with two doses of dexamethasone for mild to moderate pediatric asthma exacerbations in the emergency department. It lists enrollment of 318 and reports primary outcome denominators of 116 in each group.

The primary endpoint was participants returning for unscheduled care within 5 days after discharge. The posted counts were 14 in the single-dose group and 12 in the two-dose group; the unadjusted p-value was 0.677, and the risk-difference interval included zero. The secondary outcome was reported days until symptom resolution. The record does not report the detailed statistical plan, missing-data handling, analysis population, or an equivalence margin. Interpretation should remain limited to the posted outcomes and their stated uncertainty.