Community Care for Croup (RCT): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Community Care for Croup (RCT) (NCT01042145), a randomized phase 4 study. The primary outcome is Additional Health Care.

2. Clinical Question

The primary outcome counted a participant as having additional croup-related health care if any of the following occurred: an office visit, an emergency department visit, or hospitalization for croup care. It was assessed by self-report. The trial description states that the study compared the effectiveness of the two regimens and posed the hypothesis that multiple doses of prednisone would be superior to a single dose of dexamethasone. The posted results address the frequency of further health care, but the registry record does not report a conclusion establishing superiority.

3. Trial Design

This was a randomized, parallel-group clinical trial listed as phase 4. The registry record describes triple masking but does not specify which groups of people were masked. The trial was conducted through a practice-based research network of community pediatricians in the St. Louis area. The condition listed was croup, and the intended population was children with mild or moderate croup.

The two assigned regimens differed in both drug and schedule. The prednisone group received 2mg/kg for 3 days. The dexamethasone group received 0.6mg/kg for one day, followed by placebo for 2 days. The registry record lists enrollment of 87 participants. The primary outcome results have 40 participants in the prednisone group and 45 in the dexamethasone group; the reason these result counts do not match the overall enrollment is not reported in the registry record.

The trial began in 2009-10, had primary completion in 2011-06, and is listed as completed. Washington University School of Medicine is the listed sponsor. The registry record does not report the original sample-size justification, detailed allocation procedure, or the specific procedures used to maintain masking. These details should not be inferred from the trial's randomized and triple-masked labels.

Alongside additional health care within 11 days, the record lists secondary outcomes concerning symptom duration, disturbed sleep, parental stress, time missed from work, and reported side effects. The posted secondary results include duration of croup symptoms, nights with disturbed sleep, and parental stress; values for time missed from work and reported side effects as secondary outcomes are not reported in the registry record.

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: 103 children were assessed for eligibility. 16 were excluded prior to randomization. reasons were: did not meet inclusion criteria (10), declined to participte (6).

Overall Study

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 Additional Health Care, measured over 11 days.

The primary endpoint was the percentage of participants who had additional health care for croup within 11 days of randomization. A participant counted as having an event if they reported any office visit, emergency department visit, or hospitalization for croup care during that period. The outcome was dichotomous: each participant either met the event definition or did not.

This endpoint captures subsequent health-care use rather than symptom scores alone. Combining the listed types of care into one outcome gives a measure of whether participants sought or received additional care for croup, although it does not distinguish the type or intensity of that care. The endpoint was assessed by self-report, so the registry record does not establish that every event was confirmed from clinical records.

In the posted results, additional health care was reported for 7.0% of participants assigned to prednisone and 2.0% assigned to dexamethasone. The associated 95% confidence intervals are 1.5% to 19.9% and 0.0% to 11.5%, respectively. The comparison is therefore about the observed frequency of this defined event over the stated period, not a complete measure of all symptoms, recovery, or family experience. The registry record does not report a clinical threshold for a difference that would be considered important.

7. Results Posted in the Registry

• Dexamethasone: 2.2% (1/45) versus 7.5% (3/40) on control; risk difference -5.3 percentage points (95% CI -14.5 to 4.0), risk ratio 0.30 (0.03–2.74); unadjusted two-proportion z-test p = 0.251.

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.

Duration of Croup Symptoms

• 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:
  • Dexamethasone: mean 2.80 versus 2.20 on control; difference 0.60 (95% CI -0.29 to 1.49), standardized effect d = 0.28; z-test p = 0.184.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dexamethasone and the control. The interval gives the range of effects that remain compatible with the data.

Nights With Disturbed Sleep

• 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:
  • Dexamethasone: mean 0.68 versus 1.21 on control; difference -0.53 (95% CI -1.48 to 0.42), standardized effect d = -0.25; z-test p = 0.274.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dexamethasone and the control. The interval gives the range of effects that remain compatible with the data.

Parental Stress

• 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:
  • Dexamethasone: mean 1.39 versus 1.56 on control; difference -0.17 (95% CI -1.06 to 0.72), standardized effect d = -0.08; z-test p = 0.709.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dexamethasone and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes give a mixed descriptive pattern rather than a consistent direction across all measures. The recalculated group means for symptom duration, disturbed sleep, and parental stress do not all favor the same group. This overall pattern does not establish a broad advantage for either regimen, and it does not alter the primary outcome's uncertainty about additional health care.

The registry reports Wilcoxon (Mann-Whitney) analyses for symptom duration and parental stress, but no reported analysis for nights with disturbed sleep. Time missed from work and reported side effects are named among the secondary outcomes, while their outcome values are not reported in the registry record. This limits how comprehensively the secondary outcomes can be interpreted.

Secondary results generally carry less weight than a prespecified primary result when several outcomes are examined. General statistical explanation: testing multiple outcomes increases the opportunity for at least one result to appear unusual by chance. A multiplicity-adjustment plan can address that issue, but one is not reported in the registry record. The unadjusted secondary findings should consequently be treated as exploratory descriptions rather than as independent confirmation of the primary result.

The secondary outcome period is 12 days, whereas the primary outcome period is 11 days. The measures also capture different aspects of the illness experience and family impact. Their results can add context, but they are not interchangeable with the primary endpoint and do not resolve its uncertainty.

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

• Duration of Croup Symptoms
• Nights With Disturbed Sleep
• Parental Stress
• Time Missed From Work
• Number of Participants With Reported Side Effects

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

For a binary outcome, a risk difference compares the proportion with an event in one group with the proportion in another. Here, the recalculated comparison is dexamethasone relative to prednisone, so a negative estimate indicates a lower observed event proportion in the dexamethasone group. The estimate is -0.053. This is an unadjusted re-calculation from posted summary statistics, not a reported adjusted treatment effect.

A risk difference is expressed on the probability scale and describes an absolute contrast. It is distinct from a risk ratio or odds ratio, which express relative contrasts. The registry record also contains recalculated relative measures, but the risk difference provides the comparison used in the primary interpretation. No extra transformation of the posted estimate is needed to interpret its sign.

What does the confidence interval tell the reader?

A confidence interval describes the range of effect estimates reasonably compatible with the observed data under the analysis assumptions. The 95% interval for the recalculated primary risk difference runs from -0.145 to 0.040. Because this interval includes zero, the data do not precisely distinguish a negative risk difference from no difference or a positive risk difference. A confidence interval is not a range containing 95% of individual participants' outcomes, and it is not a statement that there is a 95% probability that the fixed treatment effect lies within this particular interval.

Why are there two p-values for the primary result?

The registry reports a Fisher Exact analysis with p = 0.34. The recalculated unadjusted risk-difference analysis has p = 0.251. Fisher's exact test is a method for assessing association in a two-group binary-outcome table. The re-calculation instead evaluates a risk difference from the posted group summaries. Different methods can yield different p-values because they use different test statistics and assumptions. The record does not report further details about how the primary confidence intervals were calculated, so a specific interval procedure should not be attributed to the registry.

Neither p-value describes the probability that the null hypothesis is true. Each measures how unusual data at least as discrepant as those observed would be under a specified null model and analysis. The p-values also do not communicate the magnitude or precision of the treatment contrast; those are addressed by the estimate and its confidence interval.

What do the continuous-outcome summaries represent?

The registry reports means and standard deviations for symptom duration, nights with disturbed sleep, and parental stress. A mean is a measure of the group's average, while a standard deviation describes spread among individual observations. A standard deviation is not the same as a confidence interval around a mean. The recalculated comparisons of means are unadjusted differences between the posted group means, with confidence intervals calculated from the posted summaries. These re-calculations should not be confused with the sponsor's reported tests, which use Wilcoxon (Mann-Whitney) methods for symptom duration and parental stress.

The Wilcoxon (Mann-Whitney) method compares the distributions or ranks of observations between groups rather than directly testing a difference in arithmetic means. The registry reports p = 0.63 for symptom duration and p = 0.51 for parental stress using this method. Those test results and the mean differences answer related, but not identical, statistical questions. The record does not report an analysis for nights with disturbed sleep.

Why can dispersion matter?

General statistical explanation: when an outcome varies more than a simple model assumes, a model that ignores that extra variation can understate uncertainty and make evidence appear more precise than it is. This issue is often called over-dispersion. It is especially relevant to count outcomes, such as nights with disturbed sleep, which may have many low values and a smaller number of high values. The registry reports means and standard deviations for that outcome, but does not report an analysis method or a model for its distribution. The summaries alone do not establish whether a particular count model or adjustment would be appropriate.

How should the reported analysis methods be distinguished?

For the primary binary endpoint, the registry's reported method is Fisher Exact. For symptom duration and parental stress, the reported method is Wilcoxon (Mann-Whitney). These methods are reported analyses; the risk-difference and mean-difference calculations are simple unadjusted re-calculations from the posted summary statistics. The registry record does not report a complete statistical analysis plan, covariate-adjusted models, interim analyses, or further details about the methods used to form the posted confidence intervals. Such details should not be assumed.

General statistical explanation: an unadjusted comparison uses the group summaries without accounting for other participant characteristics. Randomization is intended to support comparable groups on average, but the record does not report adjusted estimates. With a modest enrollment and uncertainty in the estimates, unadjusted results should be read as comparisons of the observed groups rather than as a complete account of all possible sources of variation.

11. Confidence Intervals and Precision

The primary group estimates are 7.0% for prednisone, with a 95% confidence interval from 1.5% to 19.9%, and 2.0% for dexamethasone, with a 95% confidence interval from 0.0% to 11.5%. Both intervals are wide relative to their point estimates, indicating substantial uncertainty about each group's underlying event percentage. The intervals overlap, and the recalculated confidence interval for the risk difference, -0.145 to 0.040, includes zero.

General statistical explanation: an interval's width reflects the precision of an estimate under the analysis used. Wider intervals leave a broader range of values compatible with the observed data. A confidence interval does not tell whether a difference matters clinically; that requires a threshold for importance, which is not reported in the registry record.

The point estimate favors a lower observed event percentage in the dexamethasone group, but its interval allows for a range of possible contrasts in either direction. It would therefore be misleading to describe the point estimate alone as a conclusive group difference. Conversely, the lack of a clear difference in the analysis does not establish that the groups are equivalent. An equivalence or non-inferiority conclusion would require an appropriate design and prespecified margin, neither of which is reported in the registry record.

The secondary continuous-outcome comparisons also have confidence intervals that span zero in the posted recalculations. This indicates uncertainty about the direction and size of the mean differences. The confidence intervals should be interpreted alongside the reported distributions, analysis methods, and the fact that multiple outcomes were examined; they are not guarantees about any one participant's course.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size figures are planning illustrations based on the observed effect, not the trial's original design justification. They give participants per arm for the primary and secondary comparisons, rather than total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The trial's own original design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding number per arm for a 90% chance. These are conditional planning quantities: they depend on the assumed effect, significance level, allocation, and calculation method. They are not probabilities that the trial's observed result is correct.

The rows planning for 100%, 75%, and 50% of the observed effect illustrate how the assumed effect size changes the projected sample size. A smaller effect is harder to distinguish from random variation and therefore needs more participants to reach the same target power. The listed figures are examples for planning future studies, not evidence about how likely this completed trial was to find a difference. This is not observed power.

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 = 0.075; treatment proportion p₁ = 0.022; average p̄ = 0.049.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3041 = 0.5961.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3018 = 0.2540.
4. n = (0.5961 + 0.2540)² / (-0.0528)² = 259.5, rounded up to 260 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 <- 0.075                          # control proportion
p1 <- 0.0222222222222222                          # 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(1042145)
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 = 260 (80% power), 347 (90% power)
 75% of observed effect: n per arm = 522 (80% power), 698 (90% power)
 50% of observed effect: n per arm = 1,306 (80% power), 1,748 (90% power)
power.prop.test: 259.5 
Simulated power at n = 260 per arm: 0.821 (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. Analyses Reported by the Sponsor

The registry's primary analysis is a Fisher Exact test, with p = 0.34. The recalculated unadjusted analysis gives a risk difference of -0.053, a 95% confidence interval from -0.145 to 0.040, and p = 0.251. The re-calculation uses the posted group event counts and sizes to estimate an absolute risk contrast; it is not the same reported test as Fisher Exact. Different methods can produce different p-values without indicating an inconsistency in the posted group summaries.

The registry does not report a discrepancy between the reported and recalculated primary results. The sponsor's p-value should therefore be understood as the result of the analysis method recorded in the registry, while the risk difference and its interval offer a complementary summary of magnitude and precision. Neither result establishes a definitive difference between the groups. The registry record does not provide further detail about the sponsor's confidence-interval method or an expanded statistical analysis plan, so those methods cannot be specified beyond what is recorded.

For the secondary outcomes with reported analyses, the registry lists Wilcoxon (Mann-Whitney) tests for symptom duration and parental stress. These tests are not identical to the recalculated comparisons of means. Reading both kinds of results requires keeping their distinct statistical targets in view.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes, but a plan for handling multiplicity is not reported in the registry record. Multiplicity arises when several outcomes or comparisons are examined: even if no real group differences exist, a collection of tests can make an apparently unusual result more likely to occur by chance. Whether and how to adjust for that issue depends on the prespecified analysis plan, which is not reported.

The primary outcome is identified in the record, but the registry does not report whether there were additional primary analyses, planned subgroup analyses, or a hierarchy for interpreting secondary endpoints. It also does not report interim analyses or stopping rules. No assumptions about such procedures can be made from the posted endpoint results alone.

Missing-data handling and analysis populations are also not reported in the registry record. The enrollment is 87, while the primary outcome group counts are 40 and 45. The reason for the difference between the enrollment and those reported outcome counts, and whether it reflects missing outcome data or another accounting feature, is not reported. The record does not describe imputation, exclusions, or whether the primary analysis followed an intention-to-treat population.

These omissions matter because the method used to handle unavailable outcomes and the definition of the analysis population can affect interpretation. They do not demonstrate that bias occurred; they mean that the registry record does not allow the reader to assess those aspects of the analysis in detail. The reported results should be read with that uncertainty, alongside the outcome-specific sample sizes and confidence intervals.

16. Safety Results

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

Other (non-serious) adverse events

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

The adverse-event record lists 41 participants at risk for serious adverse events in the prednisone group and 46 in the dexamethasone group. It records zero participants affected by a serious adverse event in each group. For other adverse events, the record again lists 41 and 46 participants at risk, respectively, with zero affected in each group.

These are the counts recorded in the registry, not proof that no adverse event of any kind occurred outside the recorded categories or reporting period. The registry record does not report deaths, so deaths cannot be interpreted from these entries. It also does not provide detailed event descriptions or additional follow-up information in the adverse-event results.

Safety counts should be read in the context of the numbers at risk and the scope of the registry's reporting. Zero recorded events in these groups is a descriptive result; it does not establish that an event is impossible or quantify the risk with high precision. The trial's posted adverse-event information is limited to these counts.

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

The results describe the proportion of participants who reported additional health care for croup within 11 days: 7.0% in the prednisone group and 2.0% in the dexamethasone group. The recalculated risk difference is negative for dexamethasone relative to prednisone, but its 95% confidence interval includes zero. The registry's Fisher Exact analysis also does not establish a clear difference. The observed direction and the uncertainty around it should be considered together.

These findings do not demonstrate that the regimens are equivalent. Equivalence requires a prespecified margin and an analysis designed to test whether differences fall within that margin; the registry record does not report such a design. Nor do the findings prove that either regimen is superior. The registry description states a hypothesis of prednisone superiority, but the posted primary analysis does not establish that hypothesis.

The primary outcome measures additional health-care use, based on self-report and a combined definition that includes office visits, emergency department visits, and hospitalization. It does not by itself describe the full course of symptoms or every aspect of the family's experience. Secondary measures provide some additional context, but their results are mixed and multiplicity handling is not reported.

The findings apply to the trial's studied population and setting: children with mild or moderate croup in a community pediatric practice-based research network in the St. Louis area. The record's enrollment and posted outcome counts are limited, and important details about missing data and analysis populations are not reported. The results should not be extended beyond the recorded population, outcomes, and follow-up periods without additional evidence.

In short, the posted data quantify outcomes in the randomized groups but leave substantial uncertainty about the size and direction of any underlying difference. They are not a basis for individual treatment decisions or a guarantee of an individual child's outcome.

18. Why This Trial Matters Statistically

This trial illustrates why the effect estimate, confidence interval, and p-value each contribute different information. The primary comparison has a directional point estimate, but the interval spans effects on either side of no difference. Reporting the contrast and its precision prevents the observed percentages from being read as a definitive treatment conclusion.

It also demonstrates that an absolute effect measure and a test result answer related but distinct questions. The recalculated risk difference communicates the size and direction of the observed contrast on the event-proportion scale. The registry's Fisher Exact p-value evaluates the binary-outcome data using a different method. Considering both makes the inferential limits more visible than treating a single p-value as the whole result.

The study's secondary endpoints show another practical statistical issue: a trial can measure several aspects of an illness, yet findings across those outcomes may not point in one direction. Without a reported multiplicity plan, secondary results should be interpreted cautiously. Missing information about analysis populations and outcome completeness further limits what can be inferred from the registry record.

Finally, the planning illustrations show how future sample-size requirements depend on the effect a study aims to detect. Calculations based on an observed effect are not a substitute for a prospective design justification, and smaller target effects require larger samples. Keeping those planning concepts separate from the completed trial's observed results is important for sound interpretation.

19. Limitations

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

The primary endpoint relies on self-report, and its event definition combines an office visit, emergency department visit, or hospitalization. The registry record does not report whether these events were independently verified or how reports were collected. The combined endpoint therefore does not show which type of additional care occurred or how severe the underlying episode was.

The overall enrollment is 87, while the posted primary outcome groups include 40 and 45 participants. The reason for this difference is not reported in the registry record. The record also does not explain missing outcome handling, exclusions, or the analysis population. These gaps limit assessment of whether the posted denominators represent all randomized participants for the primary comparison.

The trial compared two regimens with different drugs and dosing schedules. The results therefore concern the assigned regimens as a whole and cannot isolate the effect of drug choice from the effect of treatment duration or schedule. The registry record does not report a design intended to separate those components.

Several listed secondary outcomes do not have complete posted results: values for time missed from work and reported side effects as secondary outcomes are not reported, and no analysis is recorded for nights with disturbed sleep. Multiplicity procedures are also not reported. The primary confidence interval is broad, and the registry record does not provide a clinical importance threshold for interpreting the size of a difference.

Finally, the registry record does not report the original sample-size justification, detailed masking procedures, or a complete statistical analysis plan. These limitations do not establish that the trial was conducted improperly; they constrain how fully its design and analysis can be assessed from the posted record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Community Care for Croup (RCT) — NCT01042145.
• Registry record last updated 2014-09-15; status last verified 2014-09.
• Results first posted 2014-09-15.
• 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.

23. Record Summary

NCT01042145, titled Community Care for Croup (RCT), is a completed phase 4 randomized, triple-masked, parallel-group trial sponsored by Washington University School of Medicine. It enrolled 87 participants and compared prednisone, 2mg/kg for 3 days, with dexamethasone, 0.6mg/kg for one day followed by placebo for 2 days, for children with mild or moderate croup in a community pediatric network in the St. Louis area.

The primary endpoint was self-reported additional health care for croup within 11 days. The posted percentages were 7.0% for prednisone and 2.0% for dexamethasone. The recalculated risk-difference interval includes zero, and the registry reports a Fisher Exact p-value of 0.34. The results therefore leave uncertainty about the direction and size of any difference. The registry record does not report the original design assumptions, missing-data approach, or multiplicity plan.