Eosinophilic Esophagitis Intervention Trial-1 Food vs. 4 Food Elimination Diet Followed by Swallowed Glucocorticoids: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Eosinophilic Esophagitis Intervention Trial-1 Food vs. 4 Food Elimination Diet Followed by Swallowed Glucocorticoids (NCT02610816), a randomized phase 2, phase 3 study. The primary outcome is Change From Baseline in Pediatric EoE Symptom Score Version 2.0 (PEESS V2.0) at 12 Weeks.

2. Clinical Question

3. Trial Design

This was a completed, randomized interventional trial listed as Phase 2 and Phase 3, with an enrollment of 67. The registry identifies its model as crossover and its masking as none. The primary diet comparison was between a 1-food elimination diet and a 4-food elimination diet. In Phase 1, the 1FED group eliminated milk; the 4FED group eliminated milk, egg, wheat, and soy. The record also describes Phase 2 treatment for participants who did not respond to their initial diet: 1FED non-responders followed 4FED, and 4FED non-responders received swallowed glucocorticosteroids.

The primary outcome was change in the parent-proxy PEESS V2.0 total score from baseline to 12 weeks. The posted primary endpoint summaries include 33.0 participants in 1FED and 16.0 in 4FED. The endpoint population is described as intent to treat, including participants with at least one clinical observation after randomization. These analysis counts should not be treated as a complete account of enrollment or of participant flow; the registry record does not report the reasons participants are absent from the posted primary summaries.

The registry describes the study as open-label by listing no masking. It does not report the randomization sequence, allocation concealment procedures, treatment adherence, or the detailed order and timing of crossover phases. The original sample-size justification and the trial’s prespecified statistical analysis plan are not reported in the registry record. These omissions limit how fully the design and analysis choices can be assessed from the posted record alone.

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: 67 participants screened, 4 excluded (2 did not meet inclusion criteria, 2 met exclusion criteria), and 63 randomized

Phase 1

Reasons for not completing this period:

Phase 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: We performed intent to treat analysis including participants who had at least one clinical observation post randomization.

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 Change From Baseline in Pediatric EoE Symptom Score Version 2.0 (PEESS V2.0) at 12 Weeks, measured over Baseline and 12 weeks.

The primary endpoint is change from baseline in the Pediatric EoE Symptom Score Version 2.0 (PEESS V2.0) at 12 weeks. The questionnaire captures symptoms associated with EoE: dysphagia, gastro-esophageal reflux disease (GERD), nausea or vomiting, and pain. Scores range from 0 to 100, with higher scores indicating more frequent and/or severe symptoms. Change is calculated as the 12-week total score minus the baseline total score; therefore, a negative change indicates a reduction in reported symptoms.

The questionnaire can be completed by children with EoE ages 8-18 years and by parents for children ages 2-18 years. For the primary efficacy endpoint, the registry specifies the parent-proxy total score change from pre-treatment to post-treatment. The score is useful as a patient- and caregiver-reported measure because it represents symptoms rather than an endoscopic or tissue measurement. It gives a way to compare symptom changes across the diet groups over the stated follow-up period.

Symptom scores and histologic outcomes answer different questions. The registry lists histologic remission among secondary outcomes, but the primary endpoint is symptom change. A change in PEESS V2.0 should therefore be interpreted as a change on that symptom scale, not as a direct measure of tissue findings or as proof of a specific biological mechanism.

7. Results Posted in the Registry

• 4FED: mean -21.60 versus -14.30 on control; difference -7.30 (95% CI -17.59 to 2.99), standardized effect d = -0.43; z-test p = 0.164.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a mean change represent?

A mean change is the average of participants’ post-treatment scores minus their baseline scores. For this endpoint, lower scores indicate less frequent and/or severe symptoms, so negative mean changes correspond to decreases on the symptom scale. The posted mean changes are -14.3 for 1FED and -21.6 for 4FED. These are group summaries; they do not show the range of individual experiences or indicate that every participant’s score changed in the same direction.

The registry reports standard deviations of 17.1 for 1FED and 17.3 for 4FED. A standard deviation describes how dispersed individual changes are around a group mean. It is not the uncertainty in the group mean itself: uncertainty in an estimate also depends on the amount of information contributing to it. A group mean can be estimated with greater or lesser precision even when the observed spread is similar, depending on the data available.

What does a difference in means describe?

The unadjusted recalculation compares the 4FED mean change with the 1FED mean change. Its estimated mean difference is -7.3 units. In this direction of comparison, a negative estimate means the 4FED group’s mean change was more negative than the 1FED group’s mean change. This is a simple comparison of posted summary statistics, not the sponsor’s mixed-model estimate. It does not adjust for other variables or account for features of the trial beyond what is represented in those summaries.

The recalculated standard error for each group mean is 2.977 for 1FED and 4.325 for 4FED. A standard error describes the sampling uncertainty of an estimate under the calculation’s assumptions; it is not the spread of individual scores. These standard errors are part of the unadjusted recalculation and should not be confused with the standard deviations reported for participant changes.

Why can an interval be more informative than a single estimate?

A confidence interval gives a range of estimates compatible with the observed data under a particular statistical method and its assumptions. The recalculated interval for the mean difference runs from -17.59 to 2.991. It communicates uncertainty about the difference more directly than the point estimate alone. Because zero lies within that interval, the recalculated summaries do not distinguish clearly between no group difference and a difference in either direction. The registry record does not specify the confidence level for this recalculated interval, so a confidence level should not be inferred from the posted figures.

What does the p-value address?

A p-value measures how incompatible the observed data are with a specified null hypothesis under the statistical model used for the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The unadjusted recalculation gives p = 0.164. The sponsor’s mixed models analysis reports p = 0.04 for superiority. These values arise from different analyses, and the sponsor’s own analysis takes precedence because the record flags a discrepancy.

The registry identifies the sponsor’s method as mixed models analysis. In general, mixed models can represent repeated or otherwise related observations while allowing for differences among participants or measurement occasions. Their exact behavior depends on the model structure, the variables included, and assumptions about the data. The registry does not report enough detail about the fitted model to evaluate those choices or reproduce the sponsor’s result. It also does not give the effect estimate or interval associated with the sponsor’s p-value.

Why can summary-statistic and model-based results differ?

A simple recalculation from means, standard deviations, and group sizes is not necessarily equivalent to a model that uses participant-level observations. The analyses may use different information or account for correlation, repeated observations, or other factors differently. Those are general reasons for possible differences, not an explanation of this trial’s discrepancy: the specific reason is not reported in the registry record. For interpretation of this trial’s primary comparison, the sponsor’s reported mixed-model analysis takes precedence, while the recalculation serves as a check on the posted summaries rather than a replacement for that analysis.

What does over-dispersion mean in general?

For count outcomes, over-dispersion means the observed variability is greater than a model assumes. If ignored, uncertainty estimates can be too small and tests can appear more decisive than warranted. The primary endpoint is continuous, so over-dispersion is not the central issue for the reported mean comparison. More generally, analyses should use a model that matches the outcome and the trial’s data structure; the registry’s brief description does not allow a full assessment of model assumptions.

What can the analysis population tell us?

The registry describes the primary analysis as intent to treat among participants with at least one clinical observation after randomization. This wording indicates that the analysis was not limited solely to participants who completed every planned observation, but the record does not explain how missing outcome observations were handled, whether all randomized participants were included in every model, or whether any imputation was used. The distinction matters because conclusions can depend on which observations contribute and how missingness is addressed.

10. Confidence Intervals and Precision

The unadjusted recalculation estimates a mean difference of -7.3 PEESS V2.0 units for 4FED relative to 1FED. Its interval extends from -17.59 to 2.991. This range is wide enough to include zero and values on either side of zero. Thus, the point estimate alone should not be read as a precise determination of the direction or size of the difference. The interval expresses uncertainty in the recalculated comparison, not the distribution of individual participants’ score changes.

In general, a confidence interval is a range constructed by a statistical method to express uncertainty about an estimated quantity. The registry record does not state the confidence level for the interval accompanying the unadjusted recalculation. It is therefore best to discuss the endpoints as the posted recalculated interval without assigning a confidence percentage. The sponsor’s own mixed-model analysis reports a p-value but no estimate or interval in the registry record, so its precision cannot be assessed from that result alone.

The group summaries also show standard deviations of 17.1 for 1FED and 17.3 for 4FED, indicating variability in individual changes. Standard deviations describe spread among observations; confidence intervals and standard errors concern uncertainty in estimated quantities. They answer related but different questions. The posted standard deviations do not by themselves establish how precisely the sponsor’s model estimated its treatment contrast.

Precision is limited by the information available for the primary comparison, including the posted analysis counts of 33.0 for 1FED and 16.0 for 4FED. These counts are those attached to the primary endpoint summaries, not a substitute for the registry’s enrollment figure. The registry record does not explain the difference between enrollment and the analysis counts, nor does it provide participant-level data with which to investigate the uncertainty further.

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 participants per arm for 80% power and participants per arm for 90% power. They are not total event counts: the registry’s sample-size assumptions specify that only time-to-event displays give total events, while other displays give participants per arm. The planning calculation uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as its basis and considers planning for 100%, 75%, or 50% of that observed effect.

For planning for 100% of the observed effect, the figures are 87 participants per arm for 80% power and 117 participants per arm for 90% power. For planning for 75% of the observed effect, the figures are 155 participants per arm for 80% power and 207 participants per arm for 90% power. For planning for 50% of the observed effect, the figures are 348 participants per arm for 80% power and 465 participants per arm for 90% power.

In plain language, 80% power means the planning calculation targets an 80% chance of detecting the chosen effect under its assumptions if that effect is the true one; 90% power uses a higher detection target. A smaller effect is harder to distinguish from random variation, so the planning figures require more participants per arm when the assumed effect is reduced. These are illustrations based on the observed effect, not the original design justification. The trial’s own design assumptions are not reported in the registry record. This is not observed power.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -7.300; pooled standard deviation σ = 17.164.
2. n = 2 × (1.96 + 0.842)² × 17.164² / -7.300² = 86.8, rounded up to 87 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
delta <- -7.3                      # observed difference in means
sigma <- 17.1640829839771                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2610816)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 87 (80% power), 117 (90% power)
 75% of observed effect: n per arm = 155 (80% power), 207 (90% power)
 50% of observed effect: n per arm = 348 (80% power), 465 (90% power)
power.t.test: 87.8 
Simulated power at n = 87 per arm: 0.797 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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 sponsor reports a mixed models analysis for superiority with p = 0.04. The registry does not include the corresponding model-based effect estimate, confidence interval, detailed model specification, or further information needed to reproduce that analysis. The reported p-value is therefore the sponsor’s posted inferential result, but its magnitude alone does not show the size or precision of the estimated difference.

The unadjusted recalculation from the posted means, standard deviations, and analysis counts gives a mean difference of -7.3, an interval from -17.59 to 2.991, and p = 0.164. It is a simple calculation from group summaries and is not an alternative mixed-model fit. The record flags a discrepancy between the recalculation and the sponsor’s analysis. The reason for that discrepancy is not reported in the registry record and should not be guessed.

For this trial, the sponsor’s own analysis takes precedence. The recalculation is useful as a transparent comparison based on the posted summaries, but it does not override the sponsor’s reported model-based analysis. Since the sponsor’s effect estimate and interval are absent, the registry record does not permit a direct comparison of the magnitude or precision estimated by the two approaches.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary symptom endpoint and several secondary outcomes, including histologic remission, quality-of-life measures, endoscopic reference score, and response by milk skin prick test status. It reports seven analyses and seven posted secondary outcomes. When multiple outcomes or comparisons are examined, the chance of obtaining at least one apparently unusual result can increase. In general, multiplicity can be addressed through prespecified testing strategies or adjustment methods, but the registry record does not report whether any such approach was planned or used.

The sponsor’s reported p = 0.04 is identified as a superiority analysis. The record does not state whether this result was adjusted for multiple comparisons, whether the primary endpoint was tested in a particular sequence, or whether the analysis was prespecified in a protocol or statistical analysis plan. Those details are not reported in the registry record. Accordingly, the p-value should be read as the reported result without assuming a multiplicity procedure or an unadjusted testing framework beyond what is explicitly stated.

The primary analysis population is described as intent to treat and includes participants who had at least one clinical observation after randomization. The registry record does not explain how missing baseline or 12-week values were handled, whether participants with no post-randomization observation were excluded, or whether missing data were imputed. It does not report reasons for missing observations or analyses assessing how missingness might affect the result. The exact number contributing to every model component is also not stated.

The record does not report interim analyses, stopping rules, or the original sample-size justification. These should not be inferred from the planning illustrations, which are based on the observed effect. The available information therefore supports describing the reported analysis population and outcomes, but not a complete evaluation of the prespecified analysis plan, multiplicity control, or missing-data assumptions.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: abdominal pain (4.0%).

The registry reports serious adverse events and other adverse events separately for four treatment groups or phases. For 1FED, serious adverse events affected 1 participant among 38 at risk; other adverse events affected 5 among 38. For 4FED, serious adverse events affected 1 among 25 at risk; other adverse events affected 8 among 25. Among 1FED non-responders receiving 4FED, no serious adverse events were reported among 19 at risk, while other adverse events affected 6 among 19. Among 4FED non-responders receiving swallowed glucocorticosteroids, no serious adverse events were reported among 10 at risk, while other adverse events affected 6 among 10. No deaths were reported in any of these groups.

These counts describe the posted safety record for the listed groups; they should not be treated as a randomized comparison of all treatments. The later-phase groups consist of participants selected by their response to the initial diet, so their figures do not represent the same comparison as the initial randomized diet groups. The registry lists abdominal pain at 4.0% among the top serious adverse event terms. The record does not provide enough detail to determine event timing, severity beyond the serious/non-serious categorization, or whether events were considered related to treatment.

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

The posted primary endpoint summaries describe decreases in mean PEESS V2.0 symptom scores in both diet groups: -14.3 units for 1FED and -21.6 units for 4FED. The unadjusted recalculation estimates a difference of -7.3 units for 4FED relative to 1FED, with an interval from -17.59 to 2.991 and p = 0.164. The sponsor’s mixed-model analysis reports a superiority result with p = 0.04. Because the registry flags a discrepancy, the sponsor’s own analysis takes precedence over the simple recalculation.

These results do not establish that one diet is better or worse in a clinical sense. The sponsor’s model-based effect estimate and interval are not reported, and the recalculated interval includes zero. The registry also does not report a threshold defining a clinically meaningful change on PEESS V2.0. The evidence should therefore be described as the reported group changes and analyses, without translating them into a treatment recommendation or a definitive statement of clinical benefit.

The endpoint measures parent-proxy reports of EoE-related symptoms at 12 weeks. It is not a direct measure of histologic remission, endoscopic findings, quality of life, or outcomes beyond that follow-up. Although those measures appear among the registry’s secondary outcomes, their results are not included in the registry record for this analysis. The diet comparison also should not be conflated with the later Phase 2 treatments used after non-response.

More broadly, a p-value does not express the probability that a treatment works, and a non-significant recalculated result does not demonstrate equivalence. Interpretation depends on the analysis method, its assumptions, the precision of the effect estimate, the outcome being measured, and the missing-data and multiplicity procedures. Several of these details are not reported in the registry record.

17. Why This Trial Matters Statistically

This trial illustrates why the analysis method matters when interpreting a clinical comparison. A simple recalculation from group means, standard deviations, and analysis counts produces a different p-value from the sponsor’s mixed-model analysis. The discrepancy is explicitly present in the record, and the sponsor’s analysis takes precedence. Without the model estimate, interval, and detailed specification, readers cannot fully reconcile the results or evaluate the model’s precision from the registry record alone.

It also distinguishes the direction of a mean change from the uncertainty in a between-group difference. Both posted group means are negative, which indicates lower symptom scores at 12 weeks than at baseline on average. That fact alone does not establish the size or certainty of a difference between the diets. The recalculated interval includes zero, while the sponsor reports a superiority p-value; the contrast makes clear why a single summary statistic is not a complete account of evidence.

The record further separates the primary symptom endpoint from secondary measures and from later treatments for non-responders. These are different questions and populations. Planning figures derived from the observed effect are also not the same as the trial’s original design rationale. Taken together, these distinctions help readers assess what the record can support and where missing analytical details limit interpretation.

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 registry record does not report the detailed randomization procedure, allocation concealment, adherence, or the exact sequence and timing of the crossover phases. Although the model is identified as crossover, the posted primary results compare the two diet groups and do not provide enough detail to reconstruct all treatment transitions. Masking is listed as none, which is relevant when interpreting a symptom outcome reported by children or parents.

The primary endpoint analysis counts differ from the overall enrollment figure, and the registry does not explain participant flow or why those counts differ. The endpoint population is described as intent to treat among participants with at least one post-randomization clinical observation, but the handling of missing outcome data is not reported. The sponsor’s mixed-model estimate and interval are also absent, limiting assessment of its magnitude and precision. The reason for the discrepancy between the sponsor analysis and the unadjusted recalculation is not reported.

The registry record does not report the original sample-size justification, full statistical analysis plan, multiplicity procedures, interim analyses, or a clinically meaningful-change threshold for PEESS V2.0. The planning illustrations are based on the observed effect and cannot fill in the original design rationale. The record lists additional secondary outcomes, but their results are not included in the registry record for this analysis. These gaps restrict conclusions to the posted primary endpoint summaries, sponsor result, and safety counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Eosinophilic Esophagitis Intervention Trial-1 Food vs. 4 Food Elimination Diet Followed by Swallowed Glucocorticoids — NCT02610816.
• Registry record last updated 2018-08-27; status last verified 2018-07.
• Results first posted 2018-07-18.
• 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

NCT02610816 is a completed randomized trial comparing a 1-food elimination diet with a 4-food elimination diet for eosinophilic esophagitis. The registry lists a crossover model, no masking, Phase 2 and Phase 3, and enrollment of 67. The primary endpoint was change in parent-proxy PEESS V2.0 total score from baseline to 12 weeks.

The posted mean changes were -14.3 for 1FED and -21.6 for 4FED. The unadjusted recalculation gives a mean difference of -7.3, an interval from -17.59 to 2.991, and p = 0.164. The sponsor reports a mixed models superiority analysis with p = 0.04; because the record flags a discrepancy, the sponsor’s analysis takes precedence. The registry does not report the sponsor’s effect estimate or interval, or key details about missing-data and multiplicity handling.