Dose-Ranging Study of Oral Viscous Budesonide in Pediatrics With Eosinophilic Esophagitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dose-Ranging Study of Oral Viscous Budesonide in Pediatrics With Eosinophilic Esophagitis (NCT00762073), a randomized phase 2 study. The primary outcome is Percent of Participants Who Responded to Therapy.

2. Clinical Question

The response definition required both a reduction from baseline in the EoE clinical symptom score and a reduction in peak eosinophil count on an esophageal biopsy collected at final evaluation. The symptom component reflected six categories, including swallowing difficulty, pain, reflux-related symptoms, and food impaction. The question therefore concerns a composite of reported symptoms and a tissue measure, rather than either measure alone. The study also recorded other clinical, histologic, endoscopic, and safety outcomes, but those are distinct from the primary question.

3. Trial Design

This was a Phase 2, randomized, placebo-controlled, parallel-group, dose-ranging study in participants with eosinophilic esophagitis. The registry record reports enrollment of 82 participants and four treatment groups: placebo, low-dose budesonide, medium-dose budesonide, and high-dose budesonide. It describes masking as quadruple. The allocation ratio and the dose amounts are not reported in the registry record.

The treatment period lasted 12 weeks. Participants were scheduled for clinic visits at baseline and study weeks 2, 4, 8, and 12. The visits included clinical symptom assessment and safety evaluation, including adverse events and vital signs. Treatment was taken by mouth twice daily, once in the morning after breakfast and once in the evening at bedtime. The registry record identifies the study as completed, with a start date of 2009-01-08 and a primary completion date of 2010-04-02.

The primary analysis population was the Full Analysis Set, defined by receipt of at least one dose and evaluable post-baseline biopsy and symptom data. The primary outcome group sizes were 18 for placebo, 17 for low dose, 19 for medium dose, and 17 for high dose. These outcome denominators differ from the group sizes listed for safety, so the efficacy and safety summaries should be read using their stated populations rather than treated as interchangeable. Reasons for differences in the analysis populations are not reported in the registry record.

The registry record does not report the original sample-size justification, the planned allocation ratio, the detailed randomization procedure, or the planned statistical analysis strategy. It also does not report whether interim analyses were planned or conducted. Those omissions limit what can be concluded about the trial's original design assumptions and analysis decisions.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS), defined as participants who received at least one dose of study drug and had evaluable post-baseline esophageal biopsy and clinical symptom data.

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.

Population: The Safety Analysis Set, defined as all randomized participants who received at least one dose of double-blind study drug. Treatment group assignment was the treatment actually received. One participant in the medium dose group was enrolled and randomized then withdrew consent and did not receive study drug.

6. Primary Endpoint

The registry lists the primary outcome as Percent of Participants Who Responded to Therapy, measured over 12 weeks after the start of treatment.

The primary endpoint was the percentage of participants who responded to therapy 12 weeks after treatment began. Response required both a reduction of at least 50% from baseline in the EoE clinical symptom score and a reduction in peak eosinophil count to no more than 6 per high-power field in esophageal biopsy tissue collected at final evaluation. Because both conditions had to be met, this endpoint represents a combined clinical and histologic response.

The symptom score ranged from 0 to 18 and was assessed by a doctor across six symptom categories: heartburn; abdominal pain; waking at night with symptoms; nausea, regurgitation, or vomiting; reduced appetite or early fullness; and swallowing pain or difficulty, including food impaction. Each category was rated according to symptoms during the prior two weeks. The scale distinguished no symptoms, mild symptoms, moderate symptoms, and severe symptoms, including symptoms that interfered with daily activities or required substantial coping behaviors.

A combined endpoint is used to capture more than one aspect of disease status in a single outcome. In this case, symptom change alone would not establish the required biopsy finding, and the biopsy finding alone would not establish the required symptom change. The registry record's definition therefore makes clear that the reported response percentages refer to participants meeting both criteria, not to improvement in either criterion separately. The record does not report the rationale for selecting this particular threshold or how the endpoint was selected among possible outcomes.

7. Results Posted in the Registry

• Low Dose: 11.8% (2/17) versus 5.6% (1/18) on control; risk difference 6.2 percentage points (95% CI -12.4 to 24.8), risk ratio 2.12 (0.21–21.27); unadjusted two-proportion z-test p = 0.512.
• Medium Dose: 52.6% (10/19) versus 5.6% (1/18) on control; risk difference 47.1 percentage points (95% CI 22.3 to 71.9), risk ratio 9.47 (1.35–66.72); unadjusted two-proportion z-test p = 0.002.
• High Dose: 47.1% (8/17) versus 5.6% (1/18) on control; risk difference 41.5 percentage points (95% CI 15.5 to 67.5), risk ratio 8.47 (1.18–60.76); unadjusted two-proportion z-test p = 0.005.

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.

Percent of Participants With Histologic Response

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Low Dose: 23.5% (4/17) versus 5.6% (1/18) on control; risk difference 18.0 percentage points (95% CI -4.8 to 40.7), risk ratio 4.24 (0.52–34.20); unadjusted two-proportion z-test p = 0.129.
  • Medium Dose: 52.6% (10/19) versus 5.6% (1/18) on control; risk difference 47.1 percentage points (95% CI 22.3 to 71.9), risk ratio 9.47 (1.35–66.72); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Low Dose and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Medium Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percent of Participants With Histologic Remission

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Low Dose: 11.8% (2/17) versus 0.0% (0/18) on control; risk difference 11.8 percentage points (95% CI -3.6 to 27.1); unadjusted two-proportion z-test p = 0.134.
  • Medium Dose: 42.1% (8/19) versus 0.0% (0/18) on control; risk difference 42.1 percentage points (95% CI 19.9 to 64.3); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Low Dose and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Medium Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percent Change From Baseline in Peak Eosinophil Count

• 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:
  • Low Dose: mean -52.62 versus 7.93 on control; difference -60.55 (95% CI -106.42 to -14.68), standardized effect d = -0.86; z-test p = 0.010.
  • Medium Dose: mean -44.02 versus 7.93 on control; difference -51.95 (95% CI -107.78 to 3.88), standardized effect d = -0.60; z-test p = 0.068.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Low Dose than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Medium Dose and the control. The interval gives the range of effects that remain compatible with the data.

The available secondary results broadly suggest that some histologic outcomes varied across the dose groups, while the size and consistency of the pattern depended on the outcome. Histologic response and histologic remission are related to tissue findings, and peak eosinophil count is another biopsy-based measure. The reported changes in peak eosinophil count also show substantial variability between participants. These outcomes complement the primary endpoint, which required both symptom improvement and a biopsy threshold, but they are not substitutes for that combined response measure.

Secondary outcomes can help describe different dimensions of the condition and can add context to the primary result. They may support a coherent interpretation when they point in a similar direction, but they do not independently establish the primary endpoint's result. The registry lists additional symptom, endoscopy, and physician assessment outcomes, but results for those measures are not reported in the registry record included in the posted summaries. Their results should not be inferred from the endpoints that are reported.

Unadjusted secondary findings carry less weight because the study examined multiple outcomes and dose comparisons, and the registry record does not report a multiplicity adjustment or testing hierarchy. When many comparisons are considered, some may appear notable by chance even if there is no corresponding underlying effect. The record also does not establish which secondary analyses were prespecified or exploratory. The secondary results are therefore best treated as context for the primary finding and as observations that could inform further study, rather than as a set of separate confirmatory conclusions.

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

• Percent of Participants With Histologic Response
• Percent of Participants With Histologic Remission
• Percent Change From Baseline in Peak Eosinophil Count
• Change From Baseline in Endoscopy Score
• Percent of Participants With Clinical Response
• Percent of Participants With Clinical Remission
• Percent Change From Baseline in Eosinophilic Esophagitis (EoE) Clinical Symptom Score (CSS)
• Change From Baseline in Physician's Global Assessment Score of Disease Severity

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is binary at the participant level: each participant either met the combined response definition or did not. A percentage summarizes the share meeting that definition in each group. For comparing a treatment group with placebo, a risk difference expresses the difference between the two response proportions. A positive difference means the observed proportion was higher in the active group; a value of zero would represent equal proportions. The recalculated values use the posted group counts and are unadjusted comparisons.

What the confidence intervals describe

A confidence interval gives a range of values compatible with the observed data under the statistical method used. For a risk difference, an interval that includes zero is compatible with no difference as well as with differences in either direction. An interval entirely above zero indicates that the values in that interval are positive under that calculation. The width also matters: a wider interval reflects less precision about the size of the difference. These intervals do not remove uncertainty, and they are not a guarantee that the true value lies within the interval.

The recalculated intervals for the primary outcome are unadjusted intervals based on the posted summary counts. The registry's reported analyses instead describe logistic regression results as odds ratios. An odds ratio compares the odds of meeting the endpoint between groups; it is not the same measure as a risk difference. Logistic regression is a model-based way to analyze a binary outcome. The registry record does not report enough detail about the sponsor's model specification, covariates, or other analysis choices to reconstruct that model from the posted summary.

How to read p-values

A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions were true. It does not measure the probability that the null hypothesis is true, the size of an effect, or the likelihood of a result being reproduced. A smaller p-value is not necessarily a more clinically important finding. Interpretation should consider the estimated difference, its confidence interval, the analysis method, the study population, and the fact that multiple outcomes and comparisons were recorded.

The recalculated p-values are unadjusted. They do not account for the number of dose comparisons or the broader collection of outcomes. The sponsor reported logistic-regression p-values for the primary comparisons; those are the trial's own analyses and take precedence when they disagree with the unadjusted recalculations. Neither set of p-values, considered alone, gives a complete account of uncertainty or of the trial's design.

Why group size and analysis population matter

Percentages can change noticeably when group counts are small because each participant represents a substantial part of the observed proportion. The primary outcome denominators are the numbers with evaluable outcome data in the Full Analysis Set, not the overall enrollment count. The Full Analysis Set required receipt of at least one dose and evaluable post-baseline biopsy and symptom data. This definition excludes participants without the required evaluable information, but the registry record does not describe the reasons for any exclusions or missing outcome data.

For continuous secondary outcomes, such as percent change in peak eosinophil count, group means and standard deviations describe the observed distributions. A mean is an average, while a standard deviation describes how spread out observations are around that average. A large standard deviation relative to the mean difference can indicate substantial variability among participants. An analysis of covariance, or ANCOVA, is a regression method that can compare groups while accounting for baseline values or other included covariates. The registry record reports ANCOVA for some secondary analyses but does not specify all model details.

Some posted recalculations use standardized differences or other summaries, but these should not be confused with the sponsor's reported model results. In general, model-based and unadjusted analyses can differ because they use different assumptions and may handle baseline information differently. The registry record does not report a complete statistical analysis plan, so the distinction between prespecified and exploratory analyses cannot be established from the record.

Multiplicity and interpretation

When several outcomes, doses, and comparisons are examined, the chance of finding at least one apparently unusual result can increase. A multiplicity adjustment is a statistical approach intended to address that issue. The registry record does not report whether the trial used such an adjustment, which outcomes were designated for formal testing beyond the primary endpoint, or whether a testing hierarchy was prespecified. Accordingly, the unadjusted secondary comparisons should be treated as supportive and exploratory rather than as independent confirmation.

These methods explain what the posted summaries mean in general. They do not establish the original analysis protocol or replace the sponsor's reported analysis. The record does not report the original sample-size justification, interim-analysis plan, or detailed handling of missing data.

11. Confidence Intervals and Precision

The observed primary response percentages are based on small analyzed groups: 18 participants in the placebo group, 17 in the low-dose group, 19 in the medium-dose group, and 17 in the high-dose group. With group sizes of this scale, a small change in the number of participants meeting the definition can shift a percentage. The point estimates therefore should not be read as highly precise descriptions of the response that would necessarily be observed in another group of participants.

The recalculated 95% confidence interval for the low-dose risk difference was -0.124 to 0.248. Because it includes zero, it is compatible with no difference as well as with a difference in either direction. The corresponding intervals for medium dose, 0.223 to 0.719, and high dose, 0.155 to 0.675, lie above zero under this unadjusted calculation. Their widths also show that the exact size of the differences remains uncertain. The interval estimates uncertainty for each comparison separately; they do not account for the full set of dose comparisons and outcomes.

A confidence interval is not a prediction interval for future participants, nor does it express the probability that a particular treatment effect is true. It is an uncertainty summary conditional on the calculation method and data. Here, the recalculated intervals come from unadjusted comparisons of proportions, whereas the sponsor reported logistic-regression odds ratios without confidence intervals. Those are different statistical summaries, and the sponsor's reported analysis takes precedence if it differs from a simple recalculation. The registry record does not report confidence intervals for the sponsor's odds ratios, limiting assessment of their precision from the sponsor analysis itself.

Precision also depends on the definition of the endpoint and the analysis population. The response required both symptom and biopsy criteria, and only participants with evaluable post-baseline data entered the Full Analysis Set. The registry record does not report the amount or pattern of missing data beyond that population definition.

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 illustrations describe how many participants per arm might be needed for a future two-arm comparison under stated assumptions. These are planning illustrations based on the observed effect, not the trial's original sample-size justification; the original design assumptions are not reported in the registry record. For the comparisons in this study, the figures are participants per arm, not total participants across both arms and not total events.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for each illustration is a stated fraction of the observed effect: the full observed effect, 75% of the observed effect, or 50% of the observed effect. The 80% power column gives the number of participants per arm estimated to provide an 80% chance of detecting the specified effect under those assumptions, if the effect and assumptions hold. The 90% power column gives the corresponding estimate for a 90% chance. These are design targets, not guarantees.

The illustrations are conditional on the observed effect, which may be an imprecise estimate from small groups. A planning calculation based on a large observed effect can yield a smaller required group size than one based on a more modest effect. Smaller effects need more participants to detect under otherwise similar assumptions. The figures are therefore scenarios for planning, not proof that the completed trial had adequate power for its outcomes. This is not observed power.

The record does not report the original sample-size calculation or its assumptions, so the illustrations cannot be used to infer why the trial enrolled its participants or whether the original target was met.

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 = 0.056; treatment proportion p₁ = 0.118; average p̄ = 0.087.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3977 = 0.7796.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3953 = 0.3327.
4. n = (0.7796 + 0.3327)² / (0.0621)² = 320.9, rounded up to 321 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 <- 0.0555555555555556                          # control proportion
p1 <- 0.117647058823529                          # 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(762073)
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 = 321 (80% power), 430 (90% power)
 75% of observed effect: n per arm = 525 (80% power), 702 (90% power)
 50% of observed effect: n per arm = 1,075 (80% power), 1,438 (90% power)
power.prop.test: 320.9 
Simulated power at n = 321 per arm: 0.811 (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 reports sponsor analyses for the primary endpoint using logistic regression. For the placebo-versus-low-dose comparison, the reported odds ratio was 2.239 with p = 0.528. For placebo versus medium dose, the reported odds ratio was 18.860 with p = 0.009, and for placebo versus high dose, it was 15.009 with p = 0.017. The registry record does not provide confidence intervals for these odds ratios.

The recalculated comparisons use the posted response counts to estimate unadjusted risk differences and corresponding confidence intervals and p-values. Because these calculations use a different measure and do not reproduce the sponsor's logistic-regression model, their results are not interchangeable. The unadjusted p-values were 0.512 for low dose, 0.002 for medium dose, and 0.005 for high dose. The sponsor's p-values are close in overall pattern but do not exactly match the recalculated values.

The discrepancy flag indicates that the sponsor result and a recalculated result differ. The sponsor's own analysis takes precedence for reporting the trial's analysis. The recalculation remains useful as a transparent description based directly on the posted summary counts, but it is not a replacement for the sponsor's model. The registry record does not report sufficient detail to determine exactly which model specifications account for the differences.

15. Multiplicity, Missing Data and Analysis Populations

The trial considered a primary endpoint and multiple secondary outcomes, with comparisons across several budesonide dose groups against placebo. Testing multiple hypotheses can increase the chance of obtaining at least one apparently notable result by chance. Statistical plans sometimes address this through a multiplicity adjustment, a prespecified order of testing, or another strategy. Whether any such approach was used is not reported in the registry record.

The registry record does not report a complete statistical analysis plan, including which analyses were prespecified, the intended testing hierarchy, or how multiplicity across outcomes and dose comparisons was handled. The reported sponsor p-values and recalculated p-values should therefore not be interpreted as if they necessarily account for all statistical testing. This limitation is especially relevant to secondary outcomes, which are useful for context but should not be treated as independent confirmation without knowing the testing plan.

The Full Analysis Set included participants who received at least one dose and had evaluable post-baseline esophageal biopsy and clinical symptom data. That definition clarifies who was included in the primary endpoint analysis, but it does not explain how participants without evaluable data were handled, how much data were missing, or whether missingness differed by group. Imputation procedures, sensitivity analyses, and reasons for missing outcome data are not reported in the registry record.

The registry record also does not report whether interim analyses were planned or conducted, the original sample-size justification, or the detailed model specifications used in the sponsor's analyses. These gaps do not invalidate the posted summaries, but they limit assessment of prespecification, missing-data assumptions, and the full confirmatory status of individual comparisons. The observed results can be described, while the absent analysis details remain unresolved.

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.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: diet refusal (5.0%).

The safety summary lists participants at risk and participants with serious adverse events by group. There were no serious adverse events reported for placebo, low dose, or medium dose. In the high-dose group, 1 participant was reported with a serious adverse event among 20 at risk. The top serious adverse event term listed was Diet refusal, at 5.0%; the registry record does not clarify its group attribution in that summary.

The safety group denominators differ from the primary endpoint analysis denominators. The safety counts should therefore be read within their own stated at-risk groups, rather than compared directly with the Full Analysis Set counts. The record lists deaths as not reported in the registry record. It also records participants with other, non-serious adverse events in each group, but these figures alone do not describe event type, duration, severity, or possible relationship to study treatment.

These counts are descriptive. With the group sizes reported, the safety summary cannot establish that an event is caused by treatment or reliably characterize uncommon risks. The registry record does not provide enough detail in this summary to assess individual event narratives or comparative safety with precision.

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

The primary result describes how often participants in each study group met a particular combined symptom and biopsy definition after 12 weeks. The posted percentages were higher in the medium- and high-dose groups than in the placebo group, while the low-dose percentage was closer to the placebo percentage. The recalculated unadjusted intervals and p-values provide one way to summarize those comparisons; the sponsor's logistic-regression analyses are the trial's own reported analyses and take precedence when there is a discrepancy.

These findings do not mean that all participants in a group responded, that the observed percentages would be reproduced exactly in another study, or that a particular participant would have the same outcome. The groups were small, the confidence intervals leave uncertainty about the size of the differences, and the primary analysis required evaluable post-baseline biopsy and symptom data. The registry record does not report the details needed to assess missing-data assumptions or the original analysis plan fully.

The endpoint is also specific: a participant had to meet both the symptom-score threshold and the biopsy threshold. It does not summarize every symptom, histologic feature, endoscopic finding, or safety outcome. Some secondary results provide additional context, but multiple testing and the absence of a reported multiplicity plan mean they should be interpreted cautiously.

The results are evidence about outcomes recorded in this particular randomized study. They do not establish long-term outcomes, effects beyond the 12-week treatment period, or results for populations not described in the study. They are not medical advice and do not determine what treatment is appropriate for an individual.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares placebo with three active dose groups and reports a primary outcome that combines clinical symptoms with a biopsy measure. That design allows the observed response proportions to be considered across dose levels while keeping the endpoint definition explicit. The results also illustrate why the direction and size of an observed effect, the uncertainty interval, and the analysis method should be considered together rather than relying on a p-value alone.

The study provides a useful example of how a sponsor's model-based analysis can differ from a simple unadjusted recalculation of posted summary counts. Logistic regression reports an odds ratio, whereas the recalculation describes a risk difference. These measures answer related but distinct questions. Without full model details or confidence intervals for the sponsor's odds ratios, readers should distinguish the sponsor's reported analysis from the transparent summary-based calculation rather than treating them as interchangeable.

The small analyzed groups make precision and the choice of analysis population especially important. The study also recorded multiple secondary outcomes and comparisons, yet the registry record does not report a multiplicity strategy or complete analysis plan. That combination shows why exploratory secondary findings should be separated from the primary result and why nominal p-values need context.

Finally, the record demonstrates the limits of registry reporting. It identifies the endpoint definition and analysis population, but does not report the original sample-size rationale, detailed missing-data procedures, or full model specification. Recognizing what is documented and what remains unreported is part of interpreting clinical trial statistics responsibly.

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 analyzed groups were small, and the primary endpoint percentages are therefore subject to substantial sampling uncertainty. The recalculated confidence intervals are wide, particularly for comparisons where the observed response proportions differ, so the exact magnitude of the estimated differences is uncertain. The intervals are unadjusted and do not account for the full set of outcomes and comparisons.

The primary endpoint required both a symptom criterion and a biopsy criterion, and its analysis population required evaluable post-baseline information for both. The registry record does not report the number of participants missing outcome data, the reasons data were unavailable, or the methods used to address missingness. The safety denominators also differ from the primary outcome denominators, and reasons for that difference are not reported in the registry record.

The sponsor reported logistic-regression odds ratios without confidence intervals. Details of the model specification, including any adjustment variables, are not reported in the registry record. Consequently, the recalculated unadjusted risk differences cannot reproduce the sponsor analysis, and the sponsor estimates' precision cannot be assessed from the posted odds ratios alone.

The registry record does not report the original sample-size justification, detailed randomization procedures, interim analysis plans, or a complete statistical analysis plan. It also does not report whether multiplicity adjustments or a testing hierarchy were used. These omissions limit judgments about prespecification and the confirmatory status of secondary findings. The study's 12-week treatment period also means that the posted primary result does not describe outcomes beyond the stated assessment time.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Dose-Ranging Study of Oral Viscous Budesonide in Pediatrics With Eosinophilic Esophagitis — NCT00762073.
• Registry record last updated 2021-06-11; status last verified 2021-06.
• Results first posted 2015-10-05.
• 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

NCT00762073 was a completed, randomized, placebo-controlled, quadruple-masked, parallel-group Phase 2 dose-ranging study of oral viscous budesonide in children and adolescents with eosinophilic esophagitis. It enrolled 82 participants and compared placebo with low-, medium-, and high-dose groups over 12 weeks.

The primary endpoint was the percentage meeting a combined symptom and biopsy response definition at 12 weeks. Posted response percentages were 5.6% for placebo, 11.8% for low dose, 52.6% for medium dose, and 47.1% for high dose. Sponsor analyses used logistic regression; simple unadjusted recalculations differ, and the sponsor's own analysis takes precedence. The record does not report the original sample-size justification, full statistical analysis plan, multiplicity strategy, or detailed handling of missing data.