Trial of One Versus Two Doses of Dexamethasone for Pediatric Asthma Exacerbation: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Trial of One Versus Two Doses of Dexamethasone for Pediatric Asthma Exacerbation (NCT02725008), a randomized phase 3 study. The primary outcome is Treatment Failure.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group Phase 3 trial of one versus two doses of oral dexamethasone for acute asthma exacerbation in a pediatric emergency department. Its official title describes a double-blinded, placebo-controlled trial, while the registry’s masking classification is quadruple. The record does not identify which people were masked, so the masking categories cannot be reconciled further from the available information.

The two treatment groups differed in what participants were to take 24 hours after the emergency department visit. The Control group received dexamethasone in the department and a second dexamethasone dose to take later. The Investigational group received dexamethasone in the department and placebo to take later. The listed dexamethasone dose was 0.6 milligrams per kilogram up to 16 milligrams. The registry labels the interventions as dexamethasone and placebo.

Enrollment is listed as 99. The primary outcome results give 37 participants in the Control group and 39 in the Investigational group. These are the outcome denominators, not a replacement for the registry’s enrollment figure. The record does not explain the difference between enrollment and the primary outcome denominators, or state the analysis population used for the outcome.

The trial is marked completed. The registry lists a start of 2015-11 and primary completion of 2017-11. These dates describe the registry record and do not establish when results were analyzed or posted. The original design assumptions, including its intended sample-size justification and any planned interim analyses, are not reported in the registry record. The record lists change in symptom severity from Day 1 to Day 5 as a secondary outcome, but the secondary outcome result is not included in the registry record for this analysis.

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: 99 participants were enrolled, 2 participants underwent initial enrollment but were not randomized to a group, leaving 97 participants who were assigned to a study group.

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 Treatment Failure, measured over 5 days.

The primary endpoint is Treatment Failure, measured as a count of participants who experienced any listed failure event within 5 days. Events included an unplanned hospital admission, emergency department visit, urgent care visit, or primary care physician visit for asthma symptoms, or prescription of a course of steroids. A participant who experienced one or more of these events contributes to the outcome count; the registry defines the endpoint as participants with an event rather than as a count of visits.

This type of composite endpoint can capture several ways that an exacerbation may lead to additional care or treatment. Combining events can make an outcome more inclusive than measuring only one type of healthcare use. However, the components are not necessarily equivalent in seriousness or frequency. A combined result does not reveal which component was most influential unless component-specific results are also reported. Those component-specific outcome counts are not reported in the registry record.

The endpoint is binary at the participant level: each participant either experienced treatment failure during the stated timeframe or did not. The posted group counts are 6 of 37 in Control and 3 of 39 in Investigational. These counts describe the participants recorded with the endpoint; they do not identify the nature of each event or establish that the observed group difference is due to treatment. The registry record does not report a more detailed definition of how prescriptions or healthcare visits were verified or classified.

7. Results Posted in the Registry

• Investigational: 7.7% (3/39) versus 16.2% (6/37) on control; risk difference -8.5 percentage points (95% CI -23.0 to 6.0), risk ratio 0.47 (0.13–1.76); unadjusted two-proportion z-test p = 0.250.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the risk difference describe?

For a binary outcome, the risk in a group is the proportion of participants in that group who experienced the event. The risk difference subtracts one group’s risk from the other’s. In the recalculation, the direction is Investigational minus Control, so a negative estimate corresponds to a lower observed event proportion in Investigational. The estimate is -0.085. This is an unadjusted contrast based on the posted counts, rather than an estimate adjusted for participant characteristics or other factors.

A risk difference expresses the contrast on an absolute scale. Its confidence interval, -0.231 to 0.06, shows the range of effects compatible with the data under the method used to construct it. Values below zero favor a lower observed event proportion in Investigational on this scale, while values above zero point in the other direction. The interval crosses zero, so the observed estimate is not precise enough to distinguish a difference from no difference with confidence.

How do relative measures differ?

The relative risk compares the event risk in one group with the event risk in the other. The recalculated relative risk is 0.474, with a confidence interval from 0.128 to 1.76. A relative risk of 1 corresponds to equal event risks. The interval spans that value and also permits a range of relative effects in either direction. The odds ratio compares event odds rather than risks. The recalculated odds ratio is 0.431, with a confidence interval from 0.099 to 1.867; an odds ratio of 1 corresponds to equal odds. These relative measures are not interchangeable with a risk difference, and their numerical values cannot be directly compared as if they were on the same scale.

Odds and risks are related but distinct quantities. When events are uncommon, they can be numerically similar, but they are still defined differently. An odds ratio can also be difficult to translate into an absolute change without specifying the baseline risk. For these reasons, the risk difference and relative measures answer related but different questions. Reporting more than one scale can help readers understand the contrast, provided each is interpreted according to its definition.

What does the p-value tell a reader?

The recalculated unadjusted p-value is 0.25. In general, a p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that null hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, and it does not quantify the probability that the result will replicate. It also does not measure clinical importance. The registry’s own analysis reports p = 0.3 from a Chi-squared method. These values belong to their respective analyses and are not a direct measure of the size of the observed effect.

Whether a p-value is small or large does not remove the need to consider the estimate, confidence interval, outcome definition, study design, and limitations. In this trial, uncertainty is substantial: the confidence intervals include the no-difference value and span effects on both sides. A threshold-based reading of the p-values alone would conceal this range of plausible effects.

Why can the reported odds ratio differ from the recalculated one?

The registry reports an odds ratio of 2.32 with a 95% confidence interval from 0.54 to 10.07 and p = 0.3, using a Chi-squared analysis of the listed groups. The recalculation reports an odds ratio of 0.431 with its own interval and an unadjusted p-value of 0.25. The group direction and statistical procedure matter when comparing odds ratios. The registry’s group order is Control followed by Investigational, while the recalculated contrast is presented in the opposite direction. Reversing the direction of an odds ratio changes its interpretation; the two reported estimates should therefore not be treated as identical contrasts. The registry record does not give enough analysis detail to reconstruct its full procedure.

A Chi-squared test assesses evidence against a null association between group and binary outcome under its assumptions. The registry identifies this method for its reported analysis. General statistical methods can differ in how they calculate estimates, intervals, and p-values, particularly with sparse event counts. The registry record does not state any further details about its test implementation. The fact that two analyses use different effect measures, group ordering, or calculation procedures can yield different numerical summaries without changing the underlying observed counts.

What does randomization contribute?

Random allocation is intended to make treatment groups comparable on average, including on factors that may not be measured. That intention does not guarantee perfect balance in an individual trial, especially when outcome event counts are limited. The registry classifies the trial as randomized and parallel-group. The record does not report the randomization sequence method, allocation concealment procedure, or any baseline characteristics in the registry record, so those aspects cannot be assessed from this account.

Masking can reduce the influence of expectations on care, reporting, or outcome assessment. The official title describes the study as double blinded, and the registry classifies masking as quadruple. The record does not identify the masked roles or explain the difference between these labels. A placebo was assigned for the later dose in the one-dose group, consistent with the placebo-controlled description, but the record does not provide enough detail to assess how masking was maintained.

The primary endpoint is a composite of multiple types of healthcare use and a steroid prescription. Composite outcomes can represent a broader clinical experience, but interpretation depends on the individual components and the consistency of their ascertainment. Component-level counts, adjudication details, and further endpoint implementation details are not reported in the registry record.

10. Confidence Intervals and Precision

Confidence intervals communicate the uncertainty around an estimated effect. They are not a guarantee that the true effect lies within a particular interval, and their interpretation depends on the statistical method and assumptions. A narrow interval indicates greater precision than a wide interval on the same scale. For this trial, the recalculated risk difference is -0.085, with an interval from -0.231 to 0.06. The range includes zero and extends to estimates in both directions, so the posted counts do not determine the direction or size of the effect precisely.

The relative estimates also have broad intervals. The recalculated relative risk is 0.474, with an interval from 0.128 to 1.76. The recalculated odds ratio is 0.431, with an interval from 0.099 to 1.867. Each interval includes its scale’s no-association value. The registry’s reported odds ratio is 2.32, with a 95% confidence interval from 0.54 to 10.07, also spanning its no-association value. The registry and recalculated odds ratios use different group directions and analyses, so their intervals should be interpreted within their own definitions.

The amount of uncertainty is important: the observed group counts are limited, and only a small number of participants are recorded with treatment failure in each group. With sparse events, estimates can be sensitive to individual outcomes, and interval estimates may be wide. This does not mean the true effect is necessarily large, small, or absent. It means the registry results leave substantial uncertainty about the effect’s magnitude and direction.

A confidence interval should be read together with the point estimate and the endpoint definition. It does not resolve questions about clinical importance, bias, missing data, or generalizability. The registry record does not report a prespecified threshold for a clinically important difference, so the intervals cannot be judged against such a threshold from the available information.

11. 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 the trial’s original design assumptions. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to a stated fraction of the observed effect. The binary-outcome figures are participants per arm, not total events. Time-to-event planning displays, if present, would instead give the total number of events; the primary outcome in this trial is a binary participant count.

The 80% power column gives the planned number of participants per arm for a hypothetical study designed to have an 80% chance of detecting the specified effect under the stated assumptions, if that effect is the true one. The 90% power column gives the corresponding number for a 90% chance. These are design probabilities under a model, not probabilities that the result is true. This is not observed power.

For planning at 100% of the observed effect, the figures are 227 participants per arm for 80% power and 303 participants per arm for 90% power. Planning for 75% of the observed effect gives 434 participants per arm for 80% power and 581 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,045 participants per arm for 80% power and 1,398 participants per arm for 90% power. The pattern reflects a general principle: smaller effects are harder to detect, so a study designed to detect a smaller effect needs more participants, all else equal.

These estimates should be treated cautiously because the observed effect comes from a trial with limited outcome counts and considerable uncertainty. An observed effect can be an unstable basis for future planning. The original trial’s sample-size assumptions and justification are not reported in the registry record, so these illustrations should not be mistaken for the rationale used to design the completed trial.

12. 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 = 0.162; treatment proportion p₁ = 0.077; average p̄ = 0.120.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4588 = 0.8992.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4548 = 0.3828.
4. n = (0.8992 + 0.3828)² / (-0.0852)² = 226.2, rounded up to 227 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 <- 0.162162162162162                          # control proportion
p1 <- 0.0769230769230769                          # 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(2725008)
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 = 227 (80% power), 303 (90% power)
 75% of observed effect: n per arm = 434 (80% power), 581 (90% power)
 50% of observed effect: n per arm = 1,045 (80% power), 1,398 (90% power)
power.prop.test: 226.2 
Simulated power at n = 227 per arm: 0.815 (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.

13. Analyses Reported by the Sponsor

The registry’s reported analysis is a Chi-squared comparison, with an odds ratio of 2.32, a 95% confidence interval from 0.54 to 10.07, and p = 0.3. The unadjusted recalculation from the posted group counts gives an odds ratio of 0.431, with an interval from 0.099 to 1.867, and p = 0.25. The registry’s group order is Control followed by Investigational; the recalculated contrast is oriented Investigational relative to Control. Odds ratios reverse direction when the order of comparison is reversed, so the estimates should not be read as opposing conclusions without accounting for that orientation.

The recalculation also gives an absolute risk difference of -0.085, with an interval from -0.231 to 0.06. This measure is on a different scale from an odds ratio. The sponsor’s analysis and the recalculation are therefore complementary summaries rather than identical estimates. Their uncertainty intervals both include the no-difference value for their respective measures, and neither provides a precise estimate of the effect.

No discrepancy is flagged between the posted results and the recalculation. The registry’s own analysis remains the reported sponsor analysis; the unadjusted recalculation is a separate summary derived from the posted counts. The registry record does not provide enough detail to reproduce every aspect of the sponsor’s calculation or establish why the p-values differ.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists Treatment Failure as the primary outcome and change in symptom severity from Day 1 to Day 5 as a secondary outcome. It also lists two outcome measures and two analyses. The secondary outcome’s results are not reported in the registry record in the registry record for this analysis. Without those results and the planned testing strategy, it is not possible to assess how outcomes were prioritized or whether interpretation accounted for testing more than one outcome.

Multiplicity arises when several outcomes, comparisons, subgroups, or analyses are examined. Repeated testing can increase the chance of finding an apparently unusual result by chance. Methods to address multiplicity may include prespecifying a primary comparison, adjusting significance thresholds, or treating secondary analyses as exploratory. The trial’s statistical plan and any multiplicity adjustment are not reported in the registry record. No adjustment should be assumed from the single reported primary comparison.

The record gives enrollment of 99, while the primary outcome denominators are 37 in Control and 39 in Investigational. The registry does not report why these counts differ, whether they reflect participants with available outcome data, or the population included in the sponsor’s analysis. It also does not report how missing outcome data were handled, whether imputation was used, or whether sensitivity analyses assessed the effect of missing data. The denominators alone do not establish that participants without listed outcome counts were missing data; the reason for the difference is not stated.

The registry identifies a randomized, parallel-group design, but the analysis population is not reported in the registry record for this analysis. It is therefore not possible to determine whether the analysis followed an intention-to-treat principle, included only participants who completed treatment, or used another population definition. The record also does not provide details of protocol deviations or exclusions. These omissions limit assessment of how closely the analysis followed random assignment and how robust the estimate is to the handling of participants and outcomes.

These are reporting limitations, not evidence that a particular analysis choice was made. The registered outcome definitions, analysis population, missing-data methods, and multiplicity strategy would be needed to assess those issues more fully.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hospitalization (2.2%), respiratory failure (2.0%).

The registry’s adverse-event figures list one serious adverse event in Control among 46 at risk and one in Investigational among 51 at risk. It lists one other adverse event in each group, with the same group-specific at-risk counts. Deaths are listed as 0 in Control and 1 in Investigational. These entries describe the posted safety counts; the record does not state whether the death was considered related to treatment or provide further context in the registry record for this analysis.

The at-risk counts in the adverse-event listing differ from the primary outcome denominators. These safety counts should therefore be read in their own context rather than substituted for the denominators used for Treatment Failure. The registry record does not explain the safety analysis population or the difference in denominators. The counts do not show whether participants could contribute to more than one adverse-event category or whether the listed categories overlap.

The serious-event terms listed include Hospitalization at 2.2% and respiratory failure at 2.0%. These are the registry’s listed terms and percentages; the record does not provide enough detail to determine their relationship to the group-level serious-event counts or to assess the circumstances of each event. Sparse counts and limited context make comparative safety interpretation uncertain. The figures should not be read as proof of a causal relationship, or as a complete account of safety across all possible outcomes.

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

The primary outcome records treatment failure in 6 of 37 participants in Control and 3 of 39 in Investigational during 5 days. The unadjusted recalculated risk difference is -0.085, with an interval from -0.231 to 0.06. This is a descriptive contrast that points toward a lower observed event proportion in Investigational, but the interval spans zero and includes effects in either direction. The data do not establish a precise difference between the regimens.

The registry’s Chi-squared analysis reports an odds ratio of 2.32, a 95% confidence interval from 0.54 to 10.07, and p = 0.3. Its group ordering differs from the direction used for the recalculated risk difference, and an odds ratio is not an absolute risk difference. The sponsor’s estimate and the recalculated estimates should be interpreted by their definitions, rather than compared as if they were the same statistic. Both reflect substantial uncertainty.

The endpoint combines several kinds of unplanned care and a steroid prescription. The overall count does not reveal which component occurred, how often each occurred, or how severe the recorded events were. Component-level results are not reported in the registry record. The listed secondary outcome is change in symptom severity from Day 1 to Day 5, but its results are not reported in the registry record for this analysis.

The registry reports a completed randomized trial, but important interpretive details are not reported in the registry record, including the original sample-size justification, analysis population, handling of missing outcomes, and multiplicity strategy. The primary outcome denominators also differ from the enrollment figure, without an explanation in the record. Such gaps limit assessment of how the reported analysis relates to all enrolled participants.

These findings do not establish that either regimen is effective or ineffective, and they should not be used as medical advice. They describe the posted results for this trial’s defined comparison and outcome. A reader should consider the effect estimate, its uncertainty, the endpoint components, the analysis details, and the limits of the registry reporting together.

17. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should not be reduced to which group has fewer observed events. The posted primary counts are 6 of 37 in Control and 3 of 39 in Investigational, but the unadjusted risk difference has a confidence interval from -0.231 to 0.06. The uncertainty includes no difference and effects in either direction. The direction of the point estimate is not enough to establish a reliable group difference.

It also demonstrates why effect measures need clear orientation. The recalculated risk difference is Investigational minus Control, while the sponsor’s reported odds ratio follows the registry’s group ordering. Odds ratios and risk differences use different scales, and reversing group order reverses the direction of a relative comparison. Without attention to those definitions, unlike statistics can seem contradictory when they are not directly comparable.

The endpoint itself presents another statistical issue. Treatment Failure combines multiple forms of unplanned healthcare use and a steroid prescription. A composite can represent a broader outcome, but the aggregate count does not reveal which component contributes to the result. Component-specific counts would help readers understand what the overall endpoint captures; they are not reported in the registry record.

Finally, the enrollment figure and primary outcome denominators differ, while the analysis population and missing-data approach are not reported. These details matter because they affect how readers understand which participants contributed to the analysis and how the randomized comparison was preserved. The sample-size illustrations also show that planning depends on the effect a future study aims to detect, but the observed effect in this trial is uncertain and the original design assumptions are 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.

The primary outcome event counts are limited, and the confidence intervals are broad. As a result, estimates of both absolute and relative effects are imprecise. The primary outcome combines different types of healthcare use and treatment, but component-specific counts are not reported in the registry record. The overall result therefore cannot show which components account for the recorded events or whether the components had similar importance.

The registry lists enrollment of 99, while the primary outcome denominators are 37 in Control and 39 in Investigational. The reason for this difference is not reported in the registry record. Nor are the analysis population, missing-data handling, exclusions, protocol deviations, or sensitivity analyses described in the registry record for this analysis. This limits assessment of who contributed to the endpoint comparison and how robust it may be to analysis choices.

The registry lists a secondary symptom-severity outcome, but its results are not reported in the registry record. The statistical analysis plan, multiplicity strategy, and original sample-size justification are also not reported. The record does not state whether there were interim analyses. Consequently, it is not possible to assess whether all intended analyses are represented or how the reported analysis was prioritized.

The registry classifies masking as quadruple, while the official title describes double blinding. The record does not identify the masked roles or clarify the terminology. It also does not report age eligibility details, baseline characteristics, or detailed outcome ascertainment procedures in the registry record for this analysis. These omissions constrain evaluation of comparability, generalizability, and possible sources of measurement bias.

The adverse-event entries include limited counts and context. The safety analysis population and the relationship of listed serious-event terms to group-level counts are not explained in the registry record. The posted figures should therefore be read as reported safety data rather than a complete comparative safety assessment.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Trial of One Versus Two Doses of Dexamethasone for Pediatric Asthma Exacerbation — NCT02725008.
• Registry record last updated 2019-02-27; status last verified 2019-02.
• Results first posted 2019-02-27.
• 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

NCT02725008 is a completed randomized, parallel-group Phase 3 trial of one versus two doses of oral dexamethasone for pediatric acute asthma exacerbation in an emergency department. The one-dose group received placebo in place of the later dexamethasone dose; the comparator group received a second dexamethasone dose 24 hours after the emergency department visit.

The primary outcome was Treatment Failure within 5 days, defined by specified unplanned healthcare visits or hospital admission for asthma symptoms, or prescription of a course of steroids. The posted counts were 6 of 37 in Control and 3 of 39 in Investigational. The recalculated risk difference was -0.085, with a confidence interval from -0.231 to 0.06; the interval indicates substantial uncertainty about the direction and size of any difference.

The registry reports a Chi-squared odds ratio of 2.32, with a 95% confidence interval from 0.54 to 10.07 and p = 0.3. The analysis population, missing-data methods, multiplicity strategy, and original sample-size justification are not reported in the registry record.