Comparison of Dexlansoprazole MR to Placebo on the Ability to Maintain Healing in Subjects With Healed Erosive Esophagitis: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparison of Dexlansoprazole MR to Placebo on the Ability to Maintain Healing in Subjects With Healed Erosive Esophagitis (NCT00255151), a randomized phase 3 study. The primary outcome is Percentage of Subjects Who Maintained Complete Healing of Erosive Esophagitis as Assessed by Endoscopy - Crude Rate Analysis..

2. Clinical Question

3. Trial Design

This was a phase 3, randomized, triple-masked, parallel-group study sponsored by Takeda. It compared three assigned regimens: dexlansoprazole MR 60 mg QD, dexlansoprazole MR 90 mg QD, and placebo QD. The registry record reports enrollment of 451 and study status as completed. The study began in 2006-01, and primary completion was recorded in 2006-11.

The stated purpose was to evaluate maintenance of healing in subjects with healed erosive esophagitis. The primary outcome was assessed by endoscopy over 6 months. The analysis description identifies an intent-to-treat population drawn from participants in earlier healing studies, with endoscopically proven healed disease, at least one dose of study drug, and no gap of >7 days between the earlier studies and this trial. The description is incomplete in the registry record, so additional population criteria are not reported in the registry record.

Randomization supports comparison of assigned groups, while masking is intended to limit influences of treatment knowledge on care, assessment, and reporting. The registry record does not report allocation concealment details, the precise roles covered by triple masking, or the randomization procedure. It also does not report the original sample-size justification or the trial's prespecified statistical plan. Those omissions limit reconstruction of how design choices were made and which statistical procedures were planned before outcomes were observed.

The posted arm counts for the primary outcome were 112.0 for placebo, 152.0 for dexlansoprazole MR 60 mg QD, and 138.0 for dexlansoprazole MR 90 mg QD. These outcome-specific counts should not be confused with enrollment, and the registry does not explain all differences between enrollment and the analysis counts. Secondary diary outcomes report separate arm counts.

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: Subjects had to have endoscopically proven healed erosive esophagitis (EE) after 4 to 8 weeks of treatment with lansoprazole 30 mg once-daily (QD), dexlansoprazole modified release (MR) 60 mg QD, or dexlansoprazole MR 90 mg QD in the EE healing studies, T-EE04-084 (NCT00251693) and T-EE04-085 (NCT00251719).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The crude rate analysis was performed on intent-to-treat (ITT) subjects (subjects from Studies T-EE04-084 or T-EE04-085 with endoscopically proven healed EE who received at least 1 dose of study drug in this study and did not have a gap of \>7 days between the EE healing studies and this study) with at least one endoscopy in this maintenance 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 Percentage of Subjects Who Maintained Complete Healing of Erosive Esophagitis as Assessed by Endoscopy - Crude Rate Analysis., measured over 6 months.

The primary endpoint was the percentage of participants who maintained complete healing of erosive esophagitis, assessed by endoscopy, over 6 months. Endoscopic assessment evaluates the esophageal lining directly and provides a way to classify whether erosive disease remains healed, rather than relying only on symptoms reported in a diary. That distinction matters because symptoms and visible mucosal healing are related clinical domains but are not interchangeable measurements.

The registry describes a crude-rate analysis from baseline of this study. Participants who discontinued prematurely were considered relapsed. Thus, the endpoint combines endoscopic status with a stated rule for early discontinuation: those participants count as not maintaining healing. The record describes the primary analysis population as intent-to-treat participants meeting the stated prior-healing and study-entry conditions, although the population description is truncated.

A percentage is useful for comparing the fraction classified as maintaining complete healing across randomized groups. It does not show the timing of relapse, the duration of healing for each participant, or whether any difference is concentrated in a particular subgroup. Those questions would require other analyses, and such analyses are not reported in the registry record. The endpoint is specifically about maintaining endoscopic healing, so it should not be read as a complete measure of symptoms, quality of life, or overall clinical benefit.

7. Results Posted in the Registry

• Dexlansoprazole MR 60 mg QD: 66.4% (101/152) versus 14.3% (16/112) on control; risk difference 52.2 percentage points (95% CI 42.2 to 62.1), risk ratio 4.65 (2.91–7.42); unadjusted two-proportion z-test p = <0.001.
• Dexlansoprazole MR 90 mg QD: 64.5% (89/138) versus 14.3% (16/112) on control; risk difference 50.2 percentage points (95% CI 39.9 to 60.5), risk ratio 4.51 (2.82–7.22); unadjusted two-proportion z-test p = <0.001.

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.

Percentage of Days Without Daytime or Nighttime Heartburn as Assessed by Daily Diary-Mean.

• 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:
  • Dexlansoprazole MR 60 mg QD: mean 79.70 versus 29.50 on control; difference 50.20 (95% CI 43.28 to 57.12), standardized effect d = 1.67; z-test p = <0.001.
  • Dexlansoprazole MR 90 mg QD: mean 79.20 versus 29.50 on control; difference 49.70 (95% CI 42.75 to 56.65), standardized effect d = 1.68; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Dexlansoprazole MR 60 mg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Dexlansoprazole MR 90 mg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Days Without Nighttime Heartburn as Assessed by Daily Diary-Mean.

• 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:
  • Dexlansoprazole MR 60 mg QD: mean 87.10 versus 48.30 on control; difference 38.80 (95% CI 31.60 to 46.00), standardized effect d = 1.28; z-test p = <0.001.
  • Dexlansoprazole MR 90 mg QD: mean 85.40 versus 48.30 on control; difference 37.10 (95% CI 29.75 to 44.45), standardized effect d = 1.20; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Dexlansoprazole MR 60 mg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Dexlansoprazole MR 90 mg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes concern the percentage of days without daytime or nighttime heartburn and the percentage of days without nighttime heartburn, assessed by daily diary. The posted mean summaries follow a consistent broad pattern: the active-treatment groups have higher average symptom-free-day percentages than the placebo group. This is directionally compatible with the primary endpoint pattern, in which the active groups have higher observed rates of maintained endoscopic healing. The two outcome types nevertheless measure different things: diary reports describe symptoms across days, while the primary endpoint classifies endoscopic healing.

These secondary findings provide additional context about symptom experience, but they should not be treated as independent confirmation of the primary endpoint or as substitutes for it. The registry lists four secondary diary outcomes, including mean and median summaries, while numeric results in the record described for this analysis cover two mean outcomes. No conclusions should be extended to secondary results whose numeric values and analyses are not reported in the registry record.

The recalculated secondary comparisons are unadjusted, and the registry's sponsor-reported analyses for these outcomes are not listed. When multiple outcomes and comparisons are examined, the chance of obtaining at least one apparently strong result through random variation can increase. Prespecified multiplicity control can address that concern, but whether such a procedure was planned or used is not reported in the registry record. For that reason, unadjusted secondary p-values carry less weight than the primary result and should be interpreted as supportive, exploratory evidence rather than as a set of separate definitive claims.

Diary outcomes can also be affected by adherence to daily reporting and by differences in the number of observed diary days. The registry provides group means, standard deviations, and analysis counts for the posted mean endpoints, but fuller details about diary completion and missing diary data are not reported in the registry record. The available summaries therefore show the overall direction of the posted results without resolving how reporting completeness may have influenced them.

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

• Percentage of Days Without Daytime or Nighttime Heartburn as Assessed by Daily Diary-Median.
• Percentage of Days Without Daytime or Nighttime Heartburn as Assessed by Daily Diary-Mean.
• Percentage of Days Without Nighttime Heartburn as Assessed by Daily Diary-Median.
• Percentage of Days Without Nighttime Heartburn as Assessed by Daily Diary-Mean.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: a participant is classified as maintaining complete healing or not maintaining it under the endpoint definition. A crude rate is the number classified as maintaining healing divided by the number included in the relevant analysis, expressed as a percentage. The registry posts these rates by randomized group and states that premature discontinuation was counted as relapse. This simple rate description is easy to understand, but it does not adjust for baseline covariates or model time to relapse.

What does a risk difference describe?

A risk difference subtracts the event proportion in one group from the event proportion in another. For the recalculations, the endpoint is maintenance of healing, so a positive estimate for an active-treatment group compared with placebo means a higher observed proportion maintaining healing in that group. The risk-difference estimates are stated on the proportion scale: 0.522 for 60 mg QD versus placebo and 0.502 for 90 mg QD versus placebo. The confidence intervals describe uncertainty around those unadjusted estimates under the calculation method; they do not account for unreported design features or analysis choices.

The registry separately reports Fisher Exact tests for the primary pairwise comparisons. Fisher's exact test evaluates evidence of association in a two-by-two table and is often used for binary outcomes, particularly when cell counts may be limited. The sponsor-reported p-values for comparisons with placebo are p < 0.001, and the active-dose comparison is p = 0.805. The recalculated p-values use a different simple unadjusted approach and are p < 0.001 for both active-versus-placebo comparisons. Since the record flags a discrepancy, the sponsor's own analysis takes precedence; the recalculations are descriptive checks rather than a correction of the official reported result.

What does a confidence interval add?

A confidence interval gives a range of estimates compatible with the data under the method's assumptions. It communicates precision as well as the direction and size of an estimated contrast. A narrower interval indicates less sampling uncertainty under that method; a wider interval indicates more. It is not a range containing every participant's outcome, nor does it capture every source of uncertainty, such as unreported protocol deviations, measurement issues, or model choices.

For binary outcomes, the posted arm percentages and the risk difference are different summaries. An arm percentage describes one group, while the risk difference compares two groups on an absolute scale. Other measures, such as a risk ratio or odds ratio, compare groups on different scales and can give a different impression of relative magnitude. The posted comparison data include other relative measures, but the primary interpretation emphasizes the risk difference because it describes the absolute contrast in observed proportions.

How are the symptom outcomes summarized?

The diary endpoints are percentages of days without heartburn, summarized as means and standard deviations. A mean describes the average percentage of symptom-free days in the analyzed group. A standard deviation describes variability among participant-level values; it is not the uncertainty of the mean and is not a confidence interval. The recalculated mean differences compare group averages. The reported unadjusted recalculations have p < 0.001 for the two posted mean diary outcomes when each active group is compared with placebo.

These secondary calculations are based on posted summary statistics and are unadjusted. They should not be mistaken for the trial's full model-based results, since the registry's reported analyses for these secondary measures are not listed. The record includes four secondary outcomes, including mean and median diary summaries, but detailed posted numeric results are available for two mean outcomes in the record. Results for secondary outcomes not numerically described cannot be inferred.

Why can over-dispersion matter?

Over-dispersion arises when variability in observed data is greater than a statistical model expects. For repeated or count-type outcomes, ignoring excess variability can make standard errors too small and confidence intervals too narrow. The primary endpoint is a binary proportion, and the registry reports crude rates plus Fisher Exact tests rather than a count model. The diary summaries are percentages, with substantial observed standard deviations, but the registry does not report an over-dispersion assessment or a model for repeated daily observations. That analysis detail is not reported in the registry record, so no claim can be made about whether such dependence or extra variability was addressed.

The statistical plan, including any prespecified covariate adjustment, handling of multiplicity, and interim analyses, is not reported in the registry record. General statistical concepts explain what the reported quantities mean; they cannot fill in missing trial-specific methods. The endpoint's stated early-discontinuation rule is known, but other aspects of missing-data handling are not reported in the registry record.

11. Confidence Intervals and Precision

The posted primary endpoint confidence intervals for the group-specific crude rates are 8.4% to 22.2% for placebo QD, 58.3% to 73.9% for dexlansoprazole MR 60 mg QD, and 55.9% to 72.4% for dexlansoprazole MR 90 mg QD. These intervals indicate uncertainty around each group's estimated maintenance rate, not the range of individual participant outcomes.

For the unadjusted risk difference against placebo, the recalculated estimate for 60 mg QD is 0.522, with an interval from 0.422 to 0.621. For 90 mg QD, the estimate is 0.502, with an interval from 0.399 to 0.605. Both intervals lie on the positive side of zero, consistent with higher observed maintenance proportions in the active groups under this simple calculation. Because the sponsor's own analysis differs and the record flags a discrepancy, its reported analysis takes precedence for the official interpretation.

Confidence intervals are informative about sampling precision conditional on the calculation method and data used. They do not account for uncertainty from possible bias, outcome classification, incomplete reporting, or choices not documented in the registry. The registry does not report confidence intervals for the sponsor's Fisher Exact comparisons with placebo. The sponsor reports a 95% confidence interval for the comparison between active-dose groups, but its limits are not reported in the registry record. Accordingly, the active-dose p-value alone should not be treated as a precise estimate of the difference between doses.

More generally, interval width depends on both the observed data and the method used. A point estimate is not exact simply because it is printed to several decimal places, and a confidence interval does not guarantee that its range includes the true effect. It is a measure of statistical precision under assumptions, rather than a measure of clinical importance or certainty about every source of error.

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 effects, not the trial's original design calculation. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers planning for 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. For these non-time-to-event outcomes, the figures are participants per arm, not a total across arms or a total number of events.

The 80% power column gives the illustrative number of participants per arm for a future study to have an 80% chance of detecting the specified effect if that effect were the true one, under the listed assumptions and the calculation's model. The 90% power column describes the corresponding target for a 90% chance. These are prospective planning quantities; neither is a measure of how likely the observed result in this completed trial was to be real. This is not observed power.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller fraction of the observed effect requires more participants per arm in the listed illustrations. The observed effect can be an optimistic planning basis because it is estimated from the same trial data and may not recur at the same magnitude. The original design's intended effect, chosen power, allocation assumptions, and sample-size justification are not reported in the registry record. The illustrations therefore cannot be used to infer what the trial was designed to detect or whether the trial met its intended statistical targets.

The figures also rely on their stated normal approximation and allocation assumption. They do not account for unreported factors such as attrition expectations, multiplicity adjustments, or other design features. The illustration is best read as a sensitivity exercise showing how assumed effect size changes a planning target, rather than as a recommendation or a reconstruction of the trial protocol.

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 = 0.143; treatment proportion p₁ = 0.664; average p̄ = 0.404.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6939 = 1.3599.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5877 = 0.4946.
4. n = (1.3599 + 0.4946)² / (0.5216)² = 12.6, rounded up to 13 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 <- 0.142857142857143                          # control proportion
p1 <- 0.664473684210526                          # 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(255151)
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 = 13 (80% power), 17 (90% power)
 75% of observed effect: n per arm = 22 (80% power), 29 (90% power)
 50% of observed effect: n per arm = 45 (80% power), 60 (90% power)
power.prop.test: 12.6 
Simulated power at n = 13 per arm: 0.857 (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 Fisher Exact comparisons of placebo with each dexlansoprazole MR dose. For both active-versus-placebo comparisons, the sponsor-reported p-value is p < 0.001. For the comparison between the 60 mg QD and 90 mg QD groups, the reported p-value is p = 0.805, with a 95% confidence level identified for that analysis but no interval limits reported in the registry record.

The recalculated risk differences use the posted arm-level summary counts and are unadjusted. They produce p < 0.001 for each active dose compared with placebo, and their estimates and confidence intervals are stated separately from the sponsor's test results. The two analyses are not identical in method or reported statistic. The discrepancy flag means the sponsor's own analysis takes precedence; the recalculation should be read as a transparent, simple comparison of the posted summaries, not as an alternative official analysis.

The registry record does not explain the reason for the discrepancy or provide enough detail to reproduce all aspects of the sponsor's analysis. It does not report the analysis code, a complete statistical analysis plan, or further information about adjustments. No cause for the numerical difference should therefore be inferred. Likewise, the active-dose p-value does not establish equivalence or non-inferiority. Those conclusions require suitable prespecified margins and methods, which are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary endpoint, multiple secondary diary outcomes, and pairwise comparisons among treatment groups. It does not report whether the trial used a prespecified multiplicity procedure to control the chance of false-positive findings across those outcomes and comparisons. The sponsor's primary pairwise Fisher Exact results are reported, but the statistical analysis plan and any hierarchy or adjustment strategy are not reported in the registry record. The unadjusted recalculations should therefore be read as unadjusted, not as multiplicity-controlled confirmatory evidence.

The registry describes the primary endpoint as a crude-rate analysis and states that participants who discontinued prematurely were considered relapsed. That rule is relevant to interpreting the primary rate because it defines how early discontinuation contributes to the endpoint. Other missing-data procedures are not reported in the registry record. In particular, the record does not provide a full account of missing endoscopic assessments, missing diary days, or any sensitivity analyses examining alternative assumptions.

The primary analysis population is identified as intent-to-treat participants meeting the reported entry conditions. The text describing that population ends before all details are given. The registry reports outcome-specific arm counts, which differ between the primary endpoint and the diary summaries, but does not explain all reasons for those differences. It is not possible to determine from the registry record alone how every randomized participant was handled in each analysis.

Interim analyses, stopping rules, covariate adjustment, and other prespecified statistical methods are not reported in the registry record. These are not assumed to have been absent; their status is simply not reported. Such omissions limit assessment of whether the displayed analyses follow the original plan and how robust the findings are to alternative analytic choices.

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

The posted primary data show that a larger percentage of participants in each dexlansoprazole MR group than in the placebo group was classified as maintaining complete endoscopic healing over 6 months, under the stated rule that early discontinuation counted as relapse. The sponsor's reported tests of each active dose against placebo have p < 0.001. The direct active-dose comparison has p = 0.805, which does not establish that the doses are equivalent.

This result is about a group-level endpoint in a particular trial population: participants with healed erosive esophagitis entering a maintenance study. It does not mean that every participant assigned to either active group maintained healing, as the observed percentages make clear. Nor does the group contrast predict an individual's outcome. Differences in underlying health, treatment exposure, follow-up, and other participant-level factors are not captured by a single group percentage.

Endoscopic healing and symptom-free days are distinct outcomes. The diary results add information about reported heartburn, but they do not redefine the primary endpoint or prove that one outcome caused the other. The registry record does not establish the mechanism behind the observed group pattern, nor does it report all details needed to judge symptom reporting completeness or missing-data sensitivity.

Statistical evidence is not the same as clinical importance. A p-value describes compatibility of data with a statistical null under a test's assumptions; it does not quantify benefit for an individual or show that all sources of bias and uncertainty have been removed. Confidence intervals address sampling precision under a method, not every limitation in design or reporting. The sponsor's own analysis takes precedence over the flagged recalculations, and the registry does not provide a complete analysis plan to resolve all methodological questions.

These findings should not be generalized beyond the studied setting without further evidence. The registry record does not provide information on all possible populations, durations, or treatment contexts. It reports one completed trial and its outcomes; it does not establish broader comparative effectiveness or long-term outcomes beyond the 6-month primary timeframe.

17. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition matters as much as the numerical contrast. Maintenance of endoscopic healing is not the same as improvement in reported heartburn, and the registry also treats premature discontinuation as relapse in the primary crude-rate analysis. Those choices determine what the percentages mean and how they should be compared.

It also demonstrates the value of separating absolute comparisons from tests of statistical evidence. The recalculated risk differences describe the observed contrast in proportions, while the sponsor's Fisher Exact p-values report results from its own inferential procedure. Because the record flags a discrepancy, preserving that distinction and giving precedence to the sponsor's analysis is essential. A direct comparison between the active doses also answers a different question from either comparison with placebo; its p-value does not establish equivalence.

Finally, the record makes visible the limits of registry reporting. It contains arm-level results and selected analysis details, yet does not report a complete statistical plan, multiplicity strategy, or full missing-data account. Statistical interpretation is strongest when outcome definitions, populations, assumptions, and analysis methods can all be evaluated alongside effect estimates and uncertainty. Where those details are absent, careful boundaries on interpretation are part of the statistical result.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary population description is incomplete in the registry record, which limits assessment of exactly who entered the analysis. Although the record describes prior endoscopic healing, receipt of at least one dose, and no gap of >7 days between studies, it does not report the remainder of the inclusion description. The primary endpoint counts are also not identical to the overall enrollment, and the record does not fully explain the transition from enrollment to each outcome analysis.

The primary analysis treats premature discontinuation as relapse. This is an explicit endpoint rule, not a neutral substitute for knowing each participant's later endoscopic status. The record does not report additional sensitivity analyses using other missing-data assumptions. For diary outcomes, details about completion, missing daily entries, or handling of incomplete diaries are also not reported in the registry record.

The primary reported analysis uses Fisher Exact tests, while the simple recalculations use unadjusted summary-statistic comparisons and are flagged as discrepant. The registry does not explain that discrepancy or provide a full statistical analysis plan with which to assess methods, adjustments, or planned comparisons. The sponsor's analysis takes precedence, but the available report leaves limited scope to reproduce or audit its complete procedure.

Multiplicity handling for the multiple primary-group comparisons and secondary outcomes is not reported in the registry record. Secondary outcomes have no sponsor-reported analyses listed in the record, so their recalculated unadjusted results warrant restraint. Adverse-event counts are posted without at-risk denominators, and the record does not provide enough detail to compare event rates reliably across groups. These reporting limitations qualify interpretation but do not change the observed posted endpoint values.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Comparison of Dexlansoprazole MR to Placebo on the Ability to Maintain Healing in Subjects With Healed Erosive Esophagitis — NCT00255151.
• Registry record last updated 2012-02-03; status last verified 2012-02.
• Results first posted 2009-08-28.
• 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

NCT00255151 is a completed randomized phase 3, triple-masked, parallel-group study sponsored by Takeda. It compared dexlansoprazole MR 60 mg QD and 90 mg QD with placebo QD for maintaining healing of erosive esophagitis. Enrollment was 451, and the primary endpoint was complete healing assessed by endoscopy over 6 months.

The posted crude maintenance rates were 14.3% for placebo, 66.4% for 60 mg QD, and 64.5% for 90 mg QD. The sponsor reported Fisher Exact p-values of p < 0.001 for each active dose versus placebo and p = 0.805 for the active-dose comparison. A discrepancy is flagged for the unadjusted recalculations, so the sponsor's own analysis takes precedence. The original statistical plan, multiplicity approach, and fuller missing-data details are not reported in the registry record.