Proton Pump Inhibitor Versus Histamine-2 Receptor Antagonist for the Prevention of Recurrent Peptic Ulcers: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Proton Pump Inhibitor Versus Histamine-2 Receptor Antagonist for the Prevention of Recurrent Peptic Ulcers (NCT02551744), a randomized na study. The primary outcome is Number of Participants With Ulcer Recurrence.

2. Clinical Question

The clinical question concerns prevention of recurrent peptic ulcers among people using thienopyridines. It is a comparison of two active medicines, not a comparison with no treatment or placebo. The record describes the study as double-blind in its official title and lists quadruple masking in its design information; it does not specify which roles were masked.

The primary outcome is a count of participants who had recurrence, assessed with follow-up endoscopy at the end of the sixth month. This gives the question a defined follow-up point and an outcome tied to an examination. The registry record does not describe the diagnostic criteria for recurrence, the timing or frequency of assessments before that examination, or how participants without an endoscopy were handled. Those details are not reported in the registry record.

The posted result addresses the observed number of recurrences in each randomized group. It does not, by itself, resolve every question about comparative benefit, safety, or longer-term outcomes. The registry record posts one primary outcome and no secondary outcomes. Therefore, the posted results do not describe other clinical outcomes or outcomes beyond the six-month assessment.

3. Trial Design

The registry record describes a randomized, parallel-group trial with quadruple masking. Its official title calls it a double-blind randomized controlled trial. The record does not define the masking roles, so it is not possible to say which participants, clinicians, assessors, or other personnel were unaware of assignment. The method used to generate the random sequence and the method for concealing allocation are not reported in the registry record.

The trial enrolled 101 participants. The posted outcome counts are organized into two groups: the proton pump inhibitor group, receiving pantoprazole, and the histamine-2 receptor antagonist group, receiving famotidine. The group sizes for the primary outcome are 50 and 51, respectively. The registry record identifies peptic ulcer as the condition and thienopyridine users as the population of interest.

The treatments are described as once-daily 40 mg tablets for six months. The registry record gives the study start as 2012-07 and primary completion as 2018-07, and lists the trial status as completed. The record does not report how participants were recruited, the number or type of study sites, eligibility details beyond the broad population description, or adherence to the assigned medicines.

The primary outcome was the number of participants with ulcer recurrence, with follow-up endoscopy performed at the end of the sixth month. The stated analysis population is intention to treat. The registry record does not give further detail about how that population was defined in practice, whether all randomized participants had outcome data, or what procedures were used for missing assessments. The trial's original statistical analysis plan and its sample-size justification are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intention to treat

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 Number of Participants With Ulcer Recurrence, measured over six month.

The primary endpoint counts participants with ulcer recurrence by the six-month assessment. The registry record describes follow-up endoscopy at the end of the sixth month and identifies the analysis population as intention to treat. The posted values are counts of participants with an event, rather than a continuous measure such as a laboratory value or a time-to-event estimate.

A participant count is useful because it directly records how many people in each group met the endpoint definition during the specified follow-up. In general, a binary endpoint reduces each participant's outcome to one of two categories: the event occurred or it did not. The number with the event can then be compared across randomized groups. Such a comparison is easiest to interpret when the event definition and assessment procedures are clearly specified.

For this trial, the event is ulcer recurrence and the assessment is endoscopy at the end of the sixth month. The record does not provide the criteria used to classify an endoscopy as showing recurrence, nor does it report whether recurrence was assessed at other times. It also does not describe how an unavailable or indeterminate endoscopy was treated analytically. These details matter because the endpoint depends on both the clinical definition and how consistently participants are assessed.

The endpoint is focused on recurrence within the stated follow-up period. It does not measure the timing of recurrence, the severity of an ulcer, or outcomes after the six-month assessment. Those outcomes are not reported in the registry record.

7. Results Posted in the Registry

• Histamine-2 Receptor Antagonist Group: 13.7% (7/51) versus 2.0% (1/50) on control; risk difference 11.7 percentage points (95% CI 1.5 to 21.9), risk ratio 6.86 (0.88–53.77); unadjusted two-proportion z-test p = 0.029.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary: each participant is counted as having ulcer recurrence or not having ulcer recurrence at the specified assessment. The registry record reports the number with recurrence and the number in each group. This permits an absolute comparison of the groups' event proportions, expressed in the posted results as a risk difference. The comparison is oriented as famotidine relative to pantoprazole, so a positive difference indicates a higher observed event proportion in the famotidine group.

What does a risk difference express?

In general, a risk difference subtracts one group's event proportion from the other group's event proportion. It is an absolute measure: it describes the gap between the proportions, rather than how many times larger one proportion is than another. The posted estimate is 0.117. Its confidence interval is 0.015 to 0.219. Because the estimate is based on event counts, its precision depends in part on how much information the observed counts contain. When events are sparse, plausible differences can span a broad range even if the point estimate appears substantial.

How should the p-value be read?

The registry reports an unadjusted p-value of 0.029 for the comparison. In general, a p-value measures how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions held. It is not a measure of effect size, clinical importance, or the probability that the null hypothesis is correct. The test used to obtain the posted p-value is not reported in the registry record. The p-value is unadjusted, and the record does not report a multiplicity plan.

A p-value should be read together with the effect estimate and its confidence interval. The point estimate describes the observed comparison; the interval conveys a range of values compatible with the data under the interval procedure. In general, a confidence interval is not a guarantee that the true effect lies inside its endpoints. Its interpretation depends on the method and assumptions used to construct it. The method for the posted confidence interval is not reported in the registry record.

What do relative measures add?

The registry also lists relative risk and odds ratio comparisons. In general, a relative risk compares event proportions as a ratio, while an odds ratio compares the odds of an event. These measures express the contrast on a relative scale, unlike the risk difference's absolute scale. When event counts are small, estimates on a relative scale can be imprecise and their confidence intervals can be wide. The record's relative-effect intervals are broad, and both include the value corresponding to no relative difference. The exact estimation method for these measures is not reported in the registry record.

Different effect scales answer different questions. An absolute difference describes the size of the gap in event proportions; a relative measure describes the contrast as a ratio. Neither scale should be treated as a substitute for the other. In this trial, the absolute risk difference is the comparison for which the registry gives a confidence interval entirely above zero, while the relative-effect intervals indicate substantial uncertainty. These measures are based on the same small set of observed events, not independent evidence.

What is the role of randomization?

In general, random assignment is intended to make the groups comparable, on average, with respect to both measured and unmeasured characteristics at the start of a trial. It supports an interpretation of the between-group contrast as an effect of assignment when the trial is implemented and analyzed appropriately. The record states that allocation was randomized, but it does not report the sequence-generation or concealment procedures. It also does not report adherence, crossovers, or the extent of missing outcome data. Randomization is important, but the label alone cannot answer those implementation questions.

The record identifies the primary analysis population as intention to treat. In general, an intention-to-treat approach analyzes participants according to their randomized groups, regardless of treatment received after assignment. The registry's label does not explain how missing endoscopy results or other deviations were handled. The detailed analysis population and missing-data procedure are not reported in the registry record.

Why can sparse events affect interpretation?

With few events, each event contributes meaningfully to the observed group comparison. This can make point estimates sensitive to small changes in the event counts and can produce wide intervals, particularly for relative measures. General statistical methods can account for the distributional properties of binary data, but the specific methods used for the posted estimates are not reported. There is no basis in the registry record to attribute a particular test, correction, or model to this analysis.

The posted analysis is therefore read most directly as a comparison of the reported counts, the risk difference, its confidence interval, and the unadjusted p-value. No adjusted model, subgroup analysis, or sensitivity analysis is listed. The registry record also does not report an interim-analysis plan or stopping rule. Missing information about those procedures should not be filled in by assumption.

10. Confidence Intervals and Precision

The registry reports a risk-difference estimate of 0.117 and a confidence interval from 0.015 to 0.219 for the comparison of famotidine with pantoprazole. The interval lies above zero, which is consistent with a higher observed recurrence proportion in the famotidine group. Its width also shows that the data remain compatible with a range of absolute differences rather than a single precise value.

In general, a confidence interval reflects statistical uncertainty around an estimate under the method used to construct it. It is not a range containing a fixed percentage of individual outcomes, and it does not account automatically for biases or design limitations. The method used for this interval is not reported in the registry record. The estimate and interval should therefore be interpreted as the posted statistical comparison, without assuming details of its calculation that the record does not state.

The event counts are small: 1 participant in the pantoprazole group and 7 in the famotidine group had recurrence. Sparse outcomes limit the information available for estimating a difference. In general, fewer events tend to make estimates less stable and intervals less precise. Relative-effect intervals in the registry are also wide, underscoring uncertainty on that scale. No additional precision can be inferred from the unadjusted p-value.

The interval quantifies sampling uncertainty under statistical assumptions; it does not address whether the population enrolled represents other settings, whether outcomes were missing, or whether the assessment procedures were followed consistently. Those issues are not resolved by the interval and are not fully reported in the registry record.

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 planning illustrations based on the observed effect, not the trial's original design justification. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true one. The 90% power column gives the corresponding per-arm planning number for a 90% chance. These are design concepts, not descriptions of the probability that the observed result is correct. This is not observed power.

The planning rows consider 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For the 100% planning effect, the figures are 82 participants per arm for 80% power and 109 participants per arm for 90% power. For 75% of the observed effect, they are 121 and 161 participants per arm. For 50% of the observed effect, they are 213 and 285 participants per arm. Smaller effects require more participants for the same target power, which is why the planning figures increase as the effect being targeted becomes smaller.

These are hypothetical planning calculations, not evidence that the original trial used those assumptions or targets. The trial's original sample-size assumptions are not reported in the registry record. The figures apply to participants per arm; the event-total convention used for time-to-event outcomes does not apply to this binary endpoint.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.020; treatment proportion p₁ = 0.137; average p̄ = 0.079.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3806 = 0.7460.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3715 = 0.3127.
4. n = (0.7460 + 0.3127)² / (0.1173)² = 81.5, rounded up to 82 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 <- 0.02                          # control proportion
p1 <- 0.137254901960784                          # 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(2551744)
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 = 82 (80% power), 109 (90% power)
 75% of observed effect: n per arm = 121 (80% power), 161 (90% power)
 50% of observed effect: n per arm = 213 (80% power), 285 (90% power)
power.prop.test: 81.5 
Simulated power at n = 82 per arm: 0.842 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary outcome and no secondary outcomes. It also lists zero analyses. The posted primary comparison includes an unadjusted p-value of 0.029. The record does not describe a plan for handling multiple tests, a hierarchy of outcomes, or any multiplicity adjustment. With no secondary outcomes posted, the registry record does not permit assessment of a wider family of reported outcome tests.

In general, testing multiple hypotheses can increase the chance of obtaining at least one small p-value by chance. Prespecified testing plans and multiplicity procedures can help control that issue. No such procedure is reported in the registry record, so the unadjusted p-value should be understood as the reported result rather than as a value known to account for other planned tests. It is not possible to determine from the record whether additional analyses were planned or conducted.

The primary outcome identifies intention to treat as the population for analysis. The registry record does not explain how that population was implemented, whether every randomized participant had an evaluable endoscopy, or how missing or indeterminate assessments were handled. It does not report the number of participants with missing primary-outcome data, imputation methods, or sensitivity analyses. The posted group denominators should not be taken as proof that every randomized participant had a complete assessment.

In general, missing outcome data can affect a comparison if the availability of measurements is related to group assignment or outcome status. The consequences depend on why data are missing and on the analysis used. Without the missingness and handling details, the robustness of this result to missing data cannot be evaluated from the registry record.

The record also does not report an interim-analysis plan, stopping rule, or detailed statistical analysis plan. That absence does not establish that such procedures were absent; it means they are not reported in the registry record. The record does not describe subgroup analyses or adjusted analyses either. These limitations leave the reader without information about prespecification and the full analysis process.

14. 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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry's safety summary reports 0 serious adverse events in the pantoprazole group among 50 participants at risk and 0 in the famotidine group among 51 participants at risk. It reports 0 deaths in each group. The summary also records 1 other adverse event in each group.

These figures are counts in the posted safety summary. The registry record does not identify the type of either other adverse event, provide event descriptions, or explain whether the counts refer to participants or event episodes. No serious adverse-event terms are listed. The record does not provide additional detail about the collection period, severity grading, causality assessment, or missing safety data.

In general, the absence of a recorded serious event in a group does not establish that a treatment has no safety risks. Safety interpretation depends on the number of participants observed, duration and completeness of follow-up, event definitions, and the kinds of events collected. The posted counts describe only the safety information reported in this registry record; they do not support a comprehensive comparison of safety.

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

The result does mean that the posted six-month recurrence counts were different between the randomized groups: 1 participant in the pantoprazole group and 7 in the famotidine group had ulcer recurrence. The registry reports a positive risk difference for famotidine relative to pantoprazole, with a confidence interval above zero and an unadjusted p-value of 0.029. These statistics describe the observed primary outcome comparison.

The result does not mean that the precise size of the difference is known. The interval spans a range of possible absolute effects, and the small event counts make the estimate uncertain. The relative-effect intervals are wide as well. In general, a point estimate is not a promise that future populations will have the same difference, and a p-value is not the probability that a treatment is effective or ineffective.

The finding also does not establish effects outside the study's stated population, treatment descriptions, and six-month follow-up. The registry record does not provide detailed eligibility criteria, adherence information, recurrence definitions, missing-data handling, or longer-term outcomes. It therefore cannot establish how the result might apply to people whose characteristics or care differ from those represented in this trial.

The safety summary reports no serious adverse events or deaths in either group and one other adverse event in each group. These limited counts do not establish that the treatments have equivalent safety or that uncommon harms are absent. The types of other adverse events and the details of safety monitoring are not reported in the registry record.

Overall, the record supports a careful description of the observed six-month event counts and their statistical uncertainty. It does not provide a complete account of the analysis plan, missing outcomes, implementation, or all relevant clinical outcomes. Those limits should accompany interpretation of the posted comparison.

16. Why This Trial Matters Statistically

This trial illustrates why absolute and relative measures can tell complementary parts of a statistical story. The primary result is a risk difference, which describes the absolute gap in observed event proportions. The registry also lists relative-effect estimates. In general, the absolute scale conveys the size of the observed difference in proportion terms, while a relative scale compares groups as a ratio. Both are based on the same outcome counts and should be interpreted with their uncertainty.

The event counts are sparse: 1 recurrence in one group and 7 in the other. When events are uncommon in a small trial, estimates can be sensitive to a small number of observations, and relative measures may be especially imprecise. The broad relative-effect intervals in the registry make that uncertainty visible. The reported risk-difference interval is also important: it provides more context than the point estimate alone.

The sample-size illustrations show another general design principle: smaller effects require more participants to detect at a given power target, under the stated planning assumptions. These illustrations use fractions of the observed effect and are not evidence of the original design rationale. The original sample-size justification is not reported in the registry record.

The record also highlights the importance of reporting analysis details. It names an intention-to-treat population but does not describe missing-data handling, the test used, multiplicity procedures, or an analysis plan. Those details help readers understand how a numerical comparison was obtained and how robust it may be. Clear reporting of endpoint definitions and assessment completeness is particularly useful when the endpoint depends on a scheduled examination.

Statistically, the trial is informative as a randomized comparison with a defined six-month outcome, but its limited number of observed events and incomplete reporting constrain precision and interpretation. Distinguishing the observed result from the assumptions and design information not reported is essential to a balanced reading.

17. 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 posted outcome contains few recurrence events, which limits precision. The confidence interval for the risk difference covers a range of possible effects, and the relative-effect intervals are broad. The registry record does not provide detailed information about the estimation procedures, so their assumptions cannot be checked from the record.

The registry names intention to treat but does not report whether all randomized participants had a six-month endoscopy or how missing assessments were handled. The total enrollment is 101, while the outcome groups list 50 and 51 participants; the record does not explain whether these are all randomized participants with complete endpoint data or how the analysis population was determined. The criteria for ulcer recurrence are also not stated.

Although the record reports randomization and quadruple masking, it does not describe sequence generation, allocation concealment, or which roles were masked. It does not report adherence, treatment discontinuation, or crossover information. The official title describes the trial as double-blind, while the design information lists quadruple masking; the record does not reconcile these descriptions.

The registry provides no secondary outcomes, no analyses beyond the posted primary comparison, and no multiplicity plan. It does not report the trial's original sample-size justification, interim analyses, detailed statistical plan, or sensitivity analyses. These matters are not reported in the registry record and cannot be inferred from the posted results.

Follow-up for the primary endpoint is specified at six months. The record does not report outcomes after that time or detailed safety-event descriptions. The safety summary is therefore limited in duration and scope as presented. These reporting gaps restrict assessment of the result's precision, robustness, and broader relevance.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Proton Pump Inhibitor Versus Histamine-2 Receptor Antagonist for the Prevention of Recurrent Peptic Ulcers — NCT02551744.
• Registry record last updated 2019-08-08; status last verified 2019-06.
• Results first posted 2019-08-08.
• 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.

21. Record Summary

NCT02551744 is a completed randomized parallel-group trial comparing pantoprazole with famotidine for prevention of recurrent peptic ulcers in thienopyridine users. The record reports quadruple masking, while the official title describes a double-blind trial. It lists total enrollment of 101 and treatment descriptions of once-daily 40 mg tablets for six months.

The primary outcome was the number of participants with ulcer recurrence, assessed by follow-up endoscopy at the end of the sixth month. The stated analysis population is intention to treat. Recurrence was reported for 1 of 50 participants in the pantoprazole group and 7 of 51 in the famotidine group. The registry reports a risk difference of 0.117, a confidence interval from 0.015 to 0.219, and an unadjusted p-value of 0.029.

No secondary outcomes are posted. The safety summary reports no serious adverse events or deaths in either group and 1 other adverse event in each. The registry record does not report detailed missing-data handling, the original sample-size justification, or the full statistical analysis plan.