Effect of High-dose Oral Rabeprazole on Recurrent Bleeding After the Endoscopic Treatment of Bleeding Peptic Ulcers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of High-dose Oral Rabeprazole on Recurrent Bleeding After the Endoscopic Treatment of Bleeding Peptic Ulcers (NCT00838682), a randomized phase 4 study. The primary outcome is Rebleeding Within 3 Days.

2. Clinical Question

The central contrast is between two different early treatment strategies, not between rabeprazole and omeprazole throughout the full follow-up. Both groups received oral rabeprazole maintenance therapy from Day 4. The comparison therefore concerns the initial 3-day treatment as part of the complete regimens described in the registry record.

The primary outcome is a count of participants who experienced rebleeding by day 3. The registry reports 2 participants in the rabeprazole group and 1 in the omeprazole group, among 54 and 52 participants, respectively. These counts describe the posted observations; they do not by themselves establish that one regimen changes the chance of rebleeding. The analysis and its uncertainty, including the disagreement between the posted sponsor analysis and a simple recalculation, are important to interpreting the comparison.

The record does not report further details about the participants’ ages, ulcer characteristics, severity, or other eligibility criteria. Those characteristics cannot be inferred from the condition label or the treatment description.

3. Trial Design

This was a phase 4, randomized, open-label, parallel-group trial sponsored by The Catholic University of Korea. The registry reports enrollment of 106 participants. The study began in 2006-04, had primary completion in 2009-01, and is listed as terminated. The reason for termination is not reported in the registry record.

Participants were assigned to one of two treatment strategies after endoscopic treatment of bleeding peptic ulcers. One group received high-dose oral rabeprazole for 3 days. The other received an intravenous omeprazole bolus followed by continuous infusion for 3 days. Both groups then received oral rabeprazole maintenance therapy from Day 4 for 6 weeks. This shared later treatment means that the randomized contrast is principally between the initial treatment strategies.

The trial was not masked. Participants and clinical staff could therefore know which initial regimen was given. The registry identifies randomization but does not report the sequence-generation method, concealment procedures, or the allocation ratio planned by the investigators. The posted arm sizes were 54 and 52 participants.

The primary outcome was rebleeding within 3 days in the intention-to-treat population. Secondary outcomes listed in the posted results include rebleeding after 3 days, surgery, and death, each with a 6-week timeframe. The registry record contains a sponsor-reported analysis and results that can be compared with unadjusted recalculations from the posted counts. Details of the original statistical plan, including its sample-size rationale and any planned interim analyses, are not reported in the registry record.

Because this is an open-label trial and the number of participants is modest, interpretation depends on both the randomized design and the precision of the observed event-count comparison. Random assignment supports a comparative interpretation, but it does not remove uncertainty arising from few observed events or resolve inconsistencies between the posted analysis and the simple recalculation.

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: Patients who presented with overt or suspected upper gastrointestinal bleeding were eligible. These eligible patients were required to have an high-risk bleeding peptic ulcer on emergent endoscopy performed within 24 hours after the hospitalization. Among those, patients who achieved primary hemostasis with endoscopic hemostatic treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: intention to treat (ITT)

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 Rebleeding Within 3 Days, measured over day 3.

The primary endpoint counts participants who experienced recurrent bleeding within 3 days after endoscopic treatment of bleeding peptic ulcers. It is a binary outcome at the participant level: each participant either had a recorded rebleeding event in that timeframe or did not. The registry identifies the analysis population as intention to treat, so the stated primary comparison is based on participants in their assigned groups rather than only those who completed treatment as planned.

Early rebleeding is the primary outcome because the study’s stated objective was to compare initial treatment strategies for preventing recurrent bleeding after endoscopic treatment. The 3-day timeframe aligns with the period in which the groups received their different initial regimens. After Day 4, both groups received oral rabeprazole maintenance therapy, so the primary endpoint concentrates on the early phase when treatment differed.

The posted counts were 2 participants with rebleeding among 54 in the rabeprazole group and 1 among 52 in the omeprazole group. These are event counts, not measurements of bleeding volume or severity. A count also does not describe when within the 3-day period an event occurred. Further endpoint definitions, including how recurrent bleeding was diagnosed or adjudicated, are not reported in the registry record.

Using a prespecified time window and a participant-level event outcome makes the groups straightforward to describe. However, with few recorded events, the estimated difference can be imprecise. The endpoint therefore needs to be read together with the confidence interval and with attention to the conflicting statistical results in the registry record.

7. Results Posted in the Registry

• Omeprazole: 1.9% (1/52) versus 3.7% (2/54) on control; risk difference -1.8 percentage points (95% CI -8.0 to 4.5), risk ratio 0.52 (0.05–5.55); unadjusted two-proportion z-test p = 0.581.

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.

Rebleeding After 3 Days

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Omeprazole: 0.0% (0/52) versus 1.9% (1/54) on control; risk difference -1.9 percentage points (95% CI -5.4 to 1.7); unadjusted two-proportion z-test p = 0.324.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Omeprazole and the control. The interval gives the range of effects that remain compatible with the data.

Surgery

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Omeprazole: 0.0% (0/52) versus 3.7% (2/54) on control; risk difference -3.7 percentage points (95% CI -8.7 to 1.3); unadjusted two-proportion z-test p = 0.161.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Omeprazole and the control. The interval gives the range of effects that remain compatible with the data.

Death

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Omeprazole: 0.0% (0/52) versus 1.9% (1/54) on control; risk difference -1.9 percentage points (95% CI -5.4 to 1.7); unadjusted two-proportion z-test p = 0.324.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Omeprazole and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover rebleeding after 3 days, surgery, and death, each with a 6-week timeframe. Across these outcomes, event counts are sparse. The unadjusted recalculated comparisons do not show clear separation between groups, and their confidence intervals include no difference. Taken together, the secondary results do not provide a consistent, precise pattern that would settle the primary comparison.

These outcomes are related to the clinical course after treatment, but they are not interchangeable with the primary endpoint of rebleeding within 3 days. They use a different timeframe or measure a different event. They can add descriptive context, but a secondary endpoint should not be used to replace the primary question simply because its result appears more favourable or less favourable.

The sponsor-reported Fisher Exact results for the secondary comparisons are also listed as p <0.05. As with the primary outcome, those values differ from the unadjusted recalculations. The registry does not provide enough analysis detail to reconcile the reported results. The event counts and the sponsor’s statistical claims should therefore be kept distinct when interpreting the pattern across outcomes.

There is also a multiplicity concern. When several outcomes are tested, the chance of finding at least one result that appears statistically significant can increase. In general, adjustment procedures or a prespecified hierarchy can address this concern, but the registry does not report whether either was used. The number and priority of planned comparisons are not described beyond the posted outcomes and analyses.

For these reasons, the secondary findings carry less weight than the primary question for interpreting the trial. They are useful as additional observations, but their sparse events, unadjusted recalculations, conflicting sponsor-reported p-values, and unreported multiplicity approach all limit the strength of conclusions that can be drawn from them.

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

• Rebleeding After 3 Days
• Surgery
• Death

9. Statistical Interpretation

10. Statistical Methods Explained

The posted comparison is a two-group analysis of a binary endpoint: each participant is counted as having or not having an event within the stated timeframe. For the primary outcome, the registry reports the number with rebleeding and the total number in each randomized group. These counts allow the event proportions and between-group contrasts to be described, but the small event totals make estimates sensitive to each individual event.

What does a risk difference describe?

A risk difference compares the event proportion in one group with the event proportion in the other. In the recalculation, the contrast is expressed as omeprazole minus rabeprazole. A negative estimate therefore points toward a lower observed event proportion in the omeprazole group, while a positive estimate points toward a higher one. This direction describes the contrast; it does not by itself show that the treatment caused a difference.

The primary recalculated risk difference has a confidence interval that crosses zero. In general, zero is the value corresponding to no difference in event proportions. An interval spanning zero is compatible with a range of possible group differences, including no difference, under the method used. The interval is therefore more informative about precision than a simple statement that the observed counts differ by one participant.

Why use an exact test?

The sponsor’s posted method is Fisher Exact. As a general statistical method, Fisher’s exact test evaluates the association between group assignment and a binary outcome using the observed counts, with an exact calculation rather than relying on a large-sample approximation. It is often considered when event counts are sparse. The registry does not report the detailed test specification or the reasoning for selecting it.

The recalculated values are unadjusted re-calculations from the posted summary statistics. The primary recalculated p-value is 0.581, which differs from the sponsor’s reported p <0.05. Since the record does not provide enough detail to reproduce or diagnose the sponsor’s analysis, the two results cannot be reconciled from the registry entry alone. The sponsor’s own analysis takes precedence when identifying the sponsor-reported finding, while the recalculation is useful as a transparent check against the posted counts.

How should a p-value be read?

In general, a p-value measures how unusual data at least as discrepant as those observed would be under a specified null model and the assumptions of the test. It does not give the probability that the null hypothesis is true, the probability that chance alone caused the result, or the probability that a treatment is effective. It also does not describe the magnitude of a difference. A p-value should be considered alongside the estimated contrast, its confidence interval, study design, and data quality.

A conventional significance threshold cannot replace these considerations. The sponsor reports p <0.05 for the primary analysis, while the unadjusted recalculation is 0.581. That disagreement makes it especially important not to present a single threshold-based conclusion without identifying which analysis it comes from. The registry does not give an effect estimate or confidence interval for the sponsor’s analysis.

What does a confidence interval add?

In general, a confidence interval gives a range of values compatible with the observed data and the statistical procedure, under its assumptions. It communicates the uncertainty of an estimate rather than only whether a test crosses a threshold. A broad interval indicates limited precision: many different underlying contrasts remain compatible with the data. With few events, estimates can be particularly uncertain because changing the classification of a single participant could have a noticeable impact.

The recalculated risk-difference interval for the primary outcome includes zero and extends in both directions. It does not demonstrate that the treatments are equivalent. Equivalence requires a prespecified margin and an analysis designed to assess whether the interval falls within that margin. Neither an equivalence margin nor a noninferiority margin is reported in the registry record.

What is and is not established by the analysis?

Randomization is intended to support a fair comparison of assigned strategies by reducing systematic differences at baseline, on average. The registry states that allocation was randomized, but details of sequence generation and allocation concealment are not reported. The open-label design means that blinding was absent. The registry does not describe whether outcome assessors were masked or how rebleeding events were adjudicated.

The primary population is described as intention to treat. In general, this approach analyses participants according to their randomized assignment and preserves the comparison created by randomization. The registry does not provide a participant flow account, missing-outcome counts, or details of how missing values were handled. Thus, the label alone does not establish how every participant’s endpoint data were treated.

Finally, the posted sample-size illustrations are planning calculations based on the observed effect and specified assumptions. They are not a report of the trial’s original design rationale and are not observed power. The original sample-size justification, any interim monitoring, and the full prespecified statistical plan are not reported in the registry record. These omissions limit how fully the posted analyses can be audited.

11. Confidence Intervals and Precision

The recalculated primary risk-difference confidence interval includes zero and extends toward both a lower and a higher event proportion in the omeprazole group relative to rabeprazole. In general, a confidence interval represents the uncertainty around an estimated contrast under the statistical method used. Its width is relevant: an interval that covers a broad range of possible effects gives a less precise estimate than a narrow interval.

Here, the small number of rebleeding events limits precision. The observed counts are 2 participants in the rabeprazole group and 1 in the omeprazole group. With few events, even a small change in the observed count can materially affect an estimated contrast. The recalculated interval is consequently compatible with no difference and with effects in either direction; it does not establish that the true difference is exactly zero.

The registry’s sponsor-reported Fisher Exact analysis does not include a reported effect estimate or confidence interval. Its p-value, p <0.05, therefore cannot by itself convey the magnitude or precision of the sponsor’s estimated treatment contrast. The unadjusted recalculation reports a different p-value, 0.581, and a confidence interval that crosses zero. The registry does not explain this difference, so the precision of the sponsor’s own estimate cannot be assessed from the posted analysis details.

Confidence intervals also depend on the statistical method and assumptions used. They should not be read as a guarantee that the true effect lies within the reported range, nor as a probability statement about this particular interval. In general, they summarize the performance of a procedure over repeated applications under its assumptions.

The secondary recalculated intervals also include no difference. Their limited precision, along with the unreported handling of multiplicity, means they add little certainty to the primary comparison. Overall, the posted data leave substantial uncertainty about the size and direction of any group difference.

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 are planning calculations based on the observed primary effect, not on the trial’s original design rationale. For these binary outcomes, the listed figures are participants per arm, not total events. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to be detected is set at the stated fraction of the observed effect.

For planning at 100% of the observed effect, the illustration gives 1,353 participants per arm for 80% power and 1,811 participants per arm for 90% power. For 75% of the observed effect, it gives 2,590 participants per arm for 80% power and 3,467 participants per arm for 90% power. For 50% of the observed effect, it gives 6,242 participants per arm for 80% power and 8,356 participants per arm for 90% power.

In general, a power target describes the chance that a study designed under specified assumptions will detect an effect of a chosen size using the planned test. The 80% and 90% columns therefore represent alternative planning targets: the higher target calls for more participants under the same stated framework. Smaller effects are harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants.

These figures are not observed power. They are illustrative planning values calculated from the observed effect and should not be interpreted as a retrospective measure of whether the completed trial was adequately powered. The trial’s own sample-size justification and original design assumptions are not reported in the registry record.

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 = 0.037; treatment proportion p₁ = 0.019; average p̄ = 0.028.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2338 = 0.4583.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2335 = 0.1965.
4. n = (0.4583 + 0.1965)² / (-0.0178)² = 1,352.5, rounded up to 1,353 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 <- 0.037037037037037                          # control proportion
p1 <- 0.0192307692307692                          # 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(838682)
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 = 1,353 (80% power), 1,811 (90% power)
 75% of observed effect: n per arm = 2,590 (80% power), 3,467 (90% power)
 50% of observed effect: n per arm = 6,242 (80% power), 8,356 (90% power)
power.prop.test: 1352.5 
Simulated power at n = 1,353 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 a Fisher Exact analysis for the primary comparison and gives p <0.05. It does not provide the sponsor’s corresponding effect estimate, confidence interval, test statistic, or further information that would allow the result to be reproduced. A separate unadjusted recalculation from the posted counts gives p = 0.581. The two p-values are inconsistent, and the registry does not explain why.

Because the discrepancy is flagged in the record, the sponsor’s own analysis takes precedence when stating what the sponsor reported. That does not make the disagreement disappear: both the sponsor-reported result and the recalculated result need to be identified accurately. The recalculation is a simple check using the posted counts and should not be presented as a replacement for an analysis whose full details are unavailable.

The difference matters because the reported values imply different statistical readings. The sponsor’s result is below the conventional 0.05 threshold, whereas the recalculated result is not. Yet neither p-value alone expresses the size of the contrast. The sponsor’s estimate and interval are not reported, while the recalculated interval includes zero. Readers therefore cannot compare the precision of the sponsor’s estimate with that of the recalculation.

The same type of discrepancy appears in the reported secondary analyses, where Fisher Exact p-values are listed as p <0.05 despite the unadjusted recalculated comparisons not showing a clear difference. The underlying sponsor calculations are not described. The appropriate interpretation is to preserve the sponsor’s reported values as the sponsor’s analysis, clearly mark the conflict with the recalculations, and avoid claiming that the registry record resolves it.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes, but it does not report a multiplicity strategy. Multiplicity arises when investigators examine more than one endpoint or conduct multiple comparisons. In general, the more statistical tests considered, the greater the possibility that at least one result will cross a conventional significance threshold by chance, even if there is no underlying effect for any outcome.

Some trial analysis plans address this by adjusting significance thresholds, using a hierarchical testing sequence, or distinguishing confirmatory from exploratory outcomes. The registry does not say whether any such approach was planned or used. It also does not report whether the secondary outcomes were prespecified in a hierarchy or whether additional analyses were conducted. The posted secondary p-values should therefore not be interpreted as if they were necessarily protected against multiple testing.

The primary outcome is identified, which helps establish the main question. However, the discrepancy between the sponsor’s reported Fisher Exact result and the unadjusted recalculation remains a separate issue from multiplicity. The record does not provide sufficient details to establish whether the sponsor analysis included adjustments or used a different analysis population or procedure.

The primary endpoint is labelled intention to treat. This indicates the stated analysis population, but does not supply a complete account of participant flow, missing outcome data, withdrawals, crossovers, or protocol deviations. The number of participants with missing primary outcome data and the method used to handle any missingness are not reported in the registry record. The record also does not describe the population used for each secondary outcome.

In general, missing data can affect a comparison if the chance of missingness differs between groups or is associated with outcomes. Without information on missingness and its handling, the potential impact cannot be assessed. No imputation method, sensitivity analysis, or other missing-data procedure is reported.

Details of interim analyses and stopping rules are not reported. The trial is listed as terminated, but the reason for termination and whether the decision related to efficacy, safety, recruitment, or another consideration are not reported in the registry record. The original statistical analysis plan is also not reported, limiting assessment of how closely the posted analyses match the planned analyses.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The posted serious adverse event figures show 0 serious events among 54 participants in the rabeprazole group and 0 among 52 participants in the omeprazole group. The record also lists 2 participants with other adverse events in each group. No serious adverse event terms are listed. These are the counts recorded in the registry; they should not be read as proof that no unrecorded events occurred.

The registry’s safety fields distinguish serious adverse events from other adverse events. They do not provide further descriptions of the two other adverse events in either group, their severity, timing, or relationship to treatment. The adverse-event death fields are not reported. Separately, death is listed as a secondary outcome at 6 weeks, with 1 participant in the rabeprazole group and 0 in the omeprazole group.

These figures are descriptive and sparse. They do not establish comparative safety, particularly because the registry does not report detailed definitions, ascertainment procedures, or how missing safety information was handled. The death outcome should be kept distinct from the unreported adverse-event death fields.

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

The posted primary counts describe few rebleeding events within 3 days: 2 among 54 participants assigned to oral rabeprazole and 1 among 52 assigned to intravenous omeprazole. The recalculated unadjusted comparison has a confidence interval that includes no difference and a p-value of 0.581. Those recalculated results leave uncertainty about both the direction and size of any underlying difference.

The registry also reports a sponsor Fisher Exact result of p <0.05, which conflicts with the recalculation. The record does not provide enough detail to explain that inconsistency. The sponsor’s own result takes precedence as the sponsor-reported analysis, but it cannot be treated as if it were supported by the same numerical result as the recalculation. Both should be read with the posted event counts and the limitations of the analysis details.

The results do not establish that the strategies are equivalent. A failure to find a clear difference in a recalculation is not proof that the regimens have identical outcomes. Equivalence or noninferiority would require an appropriate design, a prespecified margin, and a suitable analysis; such a margin is not reported in the registry record.

Nor do these results determine whether either strategy is appropriate for an individual. The record describes a trial comparison, not guidance for patient care. It also does not provide sufficient participant characteristics or event definitions to judge how broadly the findings apply beyond the study population.

The shared maintenance treatment from Day 4 is important to the scope of the question. The comparison is between the specified initial 3-day treatment strategies followed by the same maintenance regimen, rather than a comparison of the drugs throughout the full 6-week period. The small number of events, open-label design, missing analysis details, and unresolved discrepancy all temper interpretation. The registry supports a description of what was recorded, but not a definitive claim about comparative effects.

18. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation should begin with the outcome counts and the design, then consider the estimate, uncertainty, and analysis details. With few binary events, a difference of one observed event can coexist with substantial uncertainty about the underlying group contrast. A p-value by itself cannot convey that uncertainty or show the size of an effect.

It also demonstrates the importance of distinguishing a sponsor-reported analysis from a transparent recalculation. The registry gives a Fisher Exact result of p <0.05, while a simple unadjusted recalculation from the posted counts gives p = 0.581. These are not minor differences in presentation; they produce different statistical readings. Without the sponsor’s estimate, interval, or further method details, the discrepancy cannot be audited from the registry record.

The primary and secondary outcomes also raise issues common to trial reporting: multiplicity, missing-data methods, analysis populations, and the link between a completed study and its original design assumptions. The registry does not report an adjustment strategy, details of missing outcome handling, or the original sample-size justification. Those omissions make it harder to understand how the posted analysis was planned and whether the displayed results reflect the full prespecified approach.

Finally, the planning illustrations underscore the difference between a prospective design calculation and a retrospective description of observed data. Their assumptions are explicit, but they are based on the observed effect and are not observed power. Keeping that distinction clear prevents a planning exercise from being mistaken for evidence about the trial’s actual ability to detect an effect.

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.

Several trial-specific limitations affect interpretation. The trial is open-label, so participants and clinical staff were not masked to the assigned initial treatment. The registry does not report whether outcome assessors were masked or whether rebleeding events were adjudicated using a prespecified independent process. The endpoint definition and event-confirmation procedures are not described.

The primary event counts are low, which limits the precision of the recalculated contrast. The confidence interval includes no difference, while the sponsor-reported Fisher Exact p-value conflicts with the recalculated p-value. The registry does not provide the sponsor’s effect estimate, confidence interval, detailed test specification, or analysis documentation needed to resolve this disagreement.

The record lists the trial as terminated but does not report why. It does not give a participant flow account, missing outcome counts, or the method used to handle missing data. Although the primary population is labelled intention to treat, the registry does not explain how that population was implemented in practice or identify the analysis population for each secondary endpoint.

The original sample-size rationale, prespecified statistical plan, interim analyses, stopping rules, and multiplicity strategy are not reported in the registry record. Thus, the available planning illustrations cannot be used to reconstruct the trial’s original design assumptions. The registry also does not provide detailed participant characteristics or enough information to assess the representativeness of the enrolled group.

Finally, all participants in both groups received oral rabeprazole maintenance therapy after the initial 3-day regimens. The findings therefore pertain to the compared treatment strategies as described, rather than to a continued head-to-head comparison of the two drugs throughout follow-up.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Effect of High-dose Oral Rabeprazole on Recurrent Bleeding After the Endoscopic Treatment of Bleeding Peptic Ulcers — NCT00838682.
• Registry record last updated 2010-09-24; status last verified 2010-08.
• Results first posted 2010-09-24.
• 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

NCT00838682 is a randomized, open-label, parallel-group phase 4 trial sponsored by The Catholic University of Korea. It enrolled 106 participants with bleeding peptic ulcers after endoscopic treatment and is listed as terminated. The primary endpoint was rebleeding within 3 days in the intention-to-treat population.

The posted primary counts were 2 of 54 participants for oral rabeprazole and 1 of 52 for intravenous omeprazole. The registry reports a Fisher Exact result of p <0.05, while the unadjusted recalculation gives p = 0.581 and a confidence interval that includes no difference. The reason for this discrepancy is not reported.

Secondary outcomes listed in the posted results were rebleeding after 3 days, surgery, and death. The registry does not report the original sample-size justification, multiplicity approach, missing-data handling, or reason for termination. The posted evidence should therefore be interpreted with attention to sparse events, uncertainty, and incomplete analysis details.