Evaluating PN 400 (VIMOVO) in Reducing Gastric Ulcers Compared to Non-steroidal Antiinflammatory Drug (NSAID) Naproxen: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluating PN 400 (VIMOVO) in Reducing Gastric Ulcers Compared to Non-steroidal Antiinflammatory Drug (NSAID) Naproxen (NCT01129011), a randomized phase 3 study. The primary outcome is Number of Participants With Gastric Ulcer Confirmed by Endoscopy.

2. Clinical Question

The registry describes a controlled comparison of PN400 with naproxen alone in people considered at risk of NSAID-associated ulcers. The primary question concerns an endoscopic finding, while the registered secondary outcomes extend to duodenal ulcers, upper gastrointestinal adverse events, heartburn symptoms, and dyspepsia measures. The clinical question is therefore broader than the primary endpoint, but the primary result addresses gastric ulcer occurrence specifically. The registry record does not report further detail about the risk criteria or the assessment schedule beyond the 6-month timeframe and the endpoint definition.

3. Trial Design

This completed phase 3 study is described as randomized, double-blind, controlled, parallel-group, and multicenter. The registry lists enrollment of 420 participants and gives 2007-09 as the start and 2008-09 as the primary completion. The posted primary endpoint results include 210 participants in each arm.

One arm received PN400 (VIMOVO), consisting of naproxen 500 mg and immediate-release esomeprazole 20 mg, dosed twice daily. The comparator arm received naproxen 500 mg twice daily. The primary endpoint was assessed over 6 months and was based on gastric ulcer confirmation by endoscopy. The registry defines an ulcer as a mucosal break at least 3 mm in diameter, measured by close application of open-endoscopic biopsy forceps, with unequivocal crater depth.

Randomization is intended to support a fair comparison by assigning participants to study groups through chance, while double blinding is intended to limit influences from knowledge of treatment assignment. These are general features of the design; the exact randomization procedure, concealment details, and blinding procedures are not reported in the registry record. Likewise, the registry record does not report the original sample-size justification, the planned handling of missing outcome data, or whether interim analyses were planned. The primary endpoint description identifies the ITT Population, but further definitions of analysis populations are not reported in the registry record.

The registry reports a completed trial and lists nine outcome measures, including the primary endpoint and secondary measures. The record describes assessments over the study period and identifies the primary timeframe as 6 months. More detailed operational information, such as the number and timing of endoscopies or how participants without an end-of-study assessment were handled, is 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.

Before assignment: Screening for eligibility and wash-out of restricted medications

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to Treat (ITT) Population

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 Gastric Ulcer Confirmed by Endoscopy, measured over 6 months.

The primary endpoint is the number of participants with a gastric ulcer confirmed by endoscopy during 6 months of treatment. The endpoint description counts a participant if a gastric ulcer occurred at any time in that period. An ulcer required a mucosal break at least 3 mm in diameter, measured by close application of open-endoscopic biopsy forceps, and an unequivocal crater depth. The stated primary analysis population is the ITT Population.

This endpoint captures a defined anatomical finding rather than symptoms alone. Endoscopic confirmation provides a specific criterion for classifying an ulcer, and counting participants makes the outcome a binary event for the arm-level comparison: a participant either met the endpoint definition or did not. It is not a count of all ulcers or a measure of ulcer size or severity.

The registry also gives a study-completion definition: a participant was considered to have completed the study if all scheduled assessments through the 6-month visit were performed, or if the endpoint of gastric ulcer confirmed by endoscopy had been reached. Details about how incomplete assessments were handled in the primary analysis are not reported in the registry record. The endpoint is used to assess the trial’s central question about gastric ulcer occurrence during treatment; it does not, by itself, describe other outcomes such as symptoms, duodenal ulcers, or adverse events.

7. Results Posted in the Registry

• Naproxen: 24.3% (51/210) versus 7.1% (15/210) on control; risk difference 17.1 percentage points (95% CI 10.4 to 23.9), risk ratio 3.40 (1.98–5.85); 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.

The Number of Participants Developing Duodenal Ulcers Throughout 6 Months of Treatment

• 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:
  • Naproxen: 5.7% (12/210) versus 1.0% (2/210) on control; risk difference 4.8 percentage points (95% CI 1.4 to 8.2), risk ratio 6.00 (1.36–26.48); unadjusted two-proportion z-test p = 0.007.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Naproxen than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Heartburn Symptom Resolution, ie no Heartburn Symptoms During the Last 7 Days Prior to the Visit

• 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:
  • Naproxen: 29.5% (62/210) versus 48.6% (102/210) on control; risk difference -19.0 percentage points (95% CI -28.2 to -9.9), risk ratio 0.61 (0.47–0.78); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Naproxen than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Improvement From Baseline in Upper Abdominal Pain and Discomfort Scores at 6 Months, Based on the Overall Treatment Evaluation for Dyspepsia Questionnaire

• 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:
  • Naproxen: 30.0% (63/210) versus 37.6% (79/210) on control; risk difference -7.6 percentage points (95% CI -16.6 to 1.4), risk ratio 0.80 (0.61–1.04); unadjusted two-proportion z-test p = 0.099.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Naproxen and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes span several domains: duodenal ulcers, upper gastrointestinal adverse events and discontinuations, heartburn symptom resolution, and dyspepsia-related measures. Across the outcomes with posted results, the broad direction is not uniform in form because the endpoints measure different events or symptoms. The posted results include patterns in which PN400 has fewer ulcer events and more participants meeting symptom-related outcomes, while at least one dyspepsia improvement comparison is less conclusive. These outcomes should not be collapsed into a single overall estimate.

The secondary findings complement the primary endpoint by addressing outcomes other than gastric ulcers, but they do not redefine the primary question. Some are endoscopic or adverse-event outcomes, while others depend on symptom assessment or questionnaire-based measures. Their measurement and interpretation therefore differ. The registry lists nine outcome measures and identifies eight as secondary outcomes; the record does not report a single combined secondary endpoint.

General statistical explanation: testing multiple outcomes creates multiple opportunities to observe a small p-value by chance, even when no underlying effects exist. Whether and how to adjust for multiplicity depends on the prespecified testing strategy and the intended interpretation of the outcomes. A multiplicity plan is not reported in the registry record. As a result, unadjusted secondary results carry less weight as confirmatory evidence than a prespecified primary analysis, particularly when many outcomes are considered. They are useful as descriptive and supportive findings, but their uncertainty and the absence of reported multiplicity procedures should remain part of their interpretation.

The secondary outcomes also differ in their definitions and scales, so a consistent direction across all measures should not be assumed. The record does not report a formal synthesis that combines these measures. The broad secondary pattern can therefore add context to the primary gastric-ulcer result, but it does not establish a single overall treatment effect across gastrointestinal outcomes.

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

• The Number of Participants With Pre-Specified NSAID-Associated Upper GI Adverse Events or Duodenal Ulcers
• The Number of Participants Discontinuing From the Study Due to NSAID-Associated Upper GI Adverse Events or to Duodenal Ulcer
• The Number of Participants Developing Duodenal Ulcers Throughout 6 Months of Treatment
• Heartburn Symptom Resolution, ie no Heartburn Symptoms During the Last 7 Days Prior to the Visit
• Improvement From Baseline in Upper Abdominal Pain and Discomfort Scores at 6 Months, Based on the Overall Treatment Evaluation for Dyspepsia Questionnaire
• Mean Change From Baseline on Pain Intensity of the Severity of Dyspepsia Assessment (SODA) Subscales
• Mean Change From Baseline on Non-Pain Symptoms of the Severity of Dyspepsia Assessment (SODA) Subscales
• Mean Change From Baseline on Satisfaction of the Severity of Dyspepsia Assessment (SODA) Subscales

9. Statistical Interpretation

10. Statistical Methods Explained

What type of outcome is the primary endpoint?

The primary outcome is a count of participants who had an endoscopically confirmed gastric ulcer during 6 months. For the comparison, each participant is classified by whether the endpoint occurred. This is a binary outcome even though the registry labels the measure as a number of participants. The arm counts are 15 and 51, with 210 participants in each arm. A binary outcome can be summarized using event counts and proportions, then compared between arms using a chosen statistical method.

General explanation: a proportion expresses the share of an arm meeting an outcome definition. A risk difference compares the proportions by subtraction and retains the original proportion scale. A risk ratio compares them by division, while an odds ratio compares the odds of the event. These measures answer related but distinct questions, and their numerical values are not interchangeable. The registry’s displayed primary analysis is described as a Cochran-Mantel-Haenszel analysis of proportions. The unadjusted recalculation is a separate summary based directly on the posted arm-level counts.

What does the reported analysis method do?

The registry names the Cochran-Mantel-Haenszel method for the primary comparison. General explanation: this method is commonly used to compare proportions while accounting for defined strata. The registry record does not identify strata or report how they were defined, so no particular adjustment or stratification details can be stated for this trial. The reported analysis gives a value of 11.9, a 95% confidence interval from 7.9 to 17.1, and p = 0.001. The registry does not explain the scale of the reported value in the posted analysis description, so it should be quoted as reported rather than treated as identical to a different effect measure.

The recalculated comparison uses the arm-level event counts without adjustment. That is useful as a transparent check of the unadjusted contrast, but it is not a substitute for the registry’s named analysis. The two summaries may differ because they use different analysis approaches or scales; the record does not provide enough methodological detail to attribute any difference to a specific reason. The recalculated p-value is p < 0.001. No adjustment for covariates or strata is part of that unadjusted recalculation.

How should p-values and confidence intervals be read?

General explanation: a p-value is calculated under a null hypothesis and a statistical model. It indicates how unusual data at least as discrepant as those observed would be if that null model and its assumptions held. It does not state the probability that a treatment effect is real, nor does it measure the probability of a particular participant’s outcome. A small p-value can be evidence against the null model, but it does not by itself show that an effect is large, precise, important, or free from bias.

A confidence interval describes the uncertainty around an estimate using a specified method. A narrower interval indicates greater precision than a wider interval on the same scale, while a wider interval leaves more values compatible with the data and method. Interpretation depends on the estimate’s scale and the analysis assumptions. The registry’s reported 95% interval belongs to its reported analysis. The recalculated risk-difference interval is a different summary and should be interpreted on its own scale. Neither interval addresses unmeasured bias or limitations in outcome ascertainment.

Why can over-dispersion matter?

General explanation: over-dispersion occurs when observed variability is greater than a statistical model expects. If a model assumes less variability than the data contain, standard errors can be too small and confidence intervals too narrow, potentially making statistical evidence appear stronger than warranted. The primary endpoint is a participant-level binary outcome, and the registry reports a Cochran-Mantel-Haenszel analysis rather than a model described in terms of dispersion. The registry record does not report an over-dispersion assessment or a specific model-based variance adjustment. This general issue should not be read as a finding that over-dispersion occurred in this trial.

What does the analysis population contribute?

The primary endpoint description identifies the ITT Population. General explanation: an intention-to-treat approach generally analyzes participants according to their randomized assignment, preserving the comparison created by randomization. The registry record does not provide a detailed operational definition of the ITT Population or explain the treatment of missing endpoint assessments, withdrawals, or protocol deviations. It is therefore not possible to determine from the registry record exactly how each such case contributed to the posted analysis.

The outcome definition also says that study completion could be reached through all scheduled assessments up to the 6-month visit or through reaching the gastric-ulcer endpoint. That definition describes completion, but does not specify a missing-data method. No further statistical-analysis plan, interim-analysis details, or adjustment for multiple testing is reported in the registry record. These omissions limit how fully the reported inferential results can be reconstructed from the registry information alone.

11. Confidence Intervals and Precision

Precision is about how narrowly the data and analysis constrain an effect estimate. The registry’s primary analysis reports a value of 11.9 with a 95% confidence interval from 7.9 to 17.1. This interval communicates uncertainty on the scale of that reported analysis. It should not be conflated with the unadjusted risk-difference estimate, which is a separate comparison calculated from the posted counts. The registry record does not explain the scale of its reported value in further detail.

The primary endpoint counts were 15 participants in the PN400 arm and 51 in the naproxen arm, out of 210 in each arm. The reported arm-level interval bounds are 4.1 to 11.5 and 18.6 to 30.7, respectively. An interval is not a set of observed values; it expresses statistical uncertainty in an estimate under a specified procedure. The registry does not state the confidence level for these arm-level bounds in the endpoint record, so they should not be described as 95% intervals.

General explanation: a confidence interval is influenced by the amount of information in the data and the variability expected under the analysis method. A confidence interval does not account automatically for every possible source of uncertainty, such as measurement error, missing data, selection effects, or deviations from the analysis assumptions. Nor does a confidence interval establish that a result is important in practical or clinical terms.

The distinction between the registry analysis and the unadjusted recalculation matters for precision as well as for the point estimate. Each method produces an interval on its own scale and under its own assumptions. The registry reports a 95% interval for its Cochran-Mantel-Haenszel analysis, while the recalculation is an unadjusted comparison. The registry record does not report enough detail to reproduce all parts of the sponsor analysis or to determine whether any additional precision adjustments were used.

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 planning figures are participants per arm for 80% power and participants per arm for 90% power. They use the primary endpoint’s observed effect as a reference and show planning illustrations for detecting 100%, 75%, or 50% of that observed effect. For 100% of the observed effect, the figures are 70 participants per arm for 80% power and 93 participants per arm for 90% power. For 75% of the observed effect, they are 111 and 148 participants per arm. For 50% of the observed effect, they are 216 and 288 participants per arm.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. These assumptions describe the planning illustration, not the original trial design. The trial’s own design assumptions and sample-size justification are not reported in the registry record. The figures are participants per arm; they are not total event counts.

In plain terms, the 80% power column describes a planning target under which a study of the listed size would have an 80% chance of detecting the specified effect if that effect and the assumptions were correct. The 90% column uses a higher chance of detection and therefore requires more participants for the same effect. Smaller effects need more participants to detect under the same assumptions. These figures are planning illustrations, not observed power; they do not measure the probability that the completed trial’s finding is true or reproduce the trial’s original planning.

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 = 0.071; treatment proportion p₁ = 0.243; average p̄ = 0.157.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5147 = 1.0088.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5002 = 0.4210.
4. n = (1.0088 + 0.4210)² / (0.1714)² = 69.6, rounded up to 70 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 <- 0.0714285714285714                          # control proportion
p1 <- 0.242857142857143                          # 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(1129011)
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 = 70 (80% power), 93 (90% power)
 75% of observed effect: n per arm = 111 (80% power), 148 (90% power)
 50% of observed effect: n per arm = 216 (80% power), 288 (90% power)
power.prop.test: 69.6 
Simulated power at n = 70 per arm: 0.818 (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 the sponsor’s primary comparison as a Cochran-Mantel-Haenszel analysis of proportions: value 11.9, 95% confidence interval from 7.9 to 17.1, and p = 0.001. This is the trial’s reported analysis. The separate recalculation uses the posted arm-level counts to make an unadjusted risk-difference comparison and gives p < 0.001. The recalculation is a simple check based on summary counts; it does not reproduce the named Cochran-Mantel-Haenszel method.

Because the reported analysis and the recalculation are not the same statistical summary, their values and intervals should not be treated as directly interchangeable. The registry record does not provide sufficient detail about the reported value’s scale, the strata used, or other analysis specifications to explain the relationship more fully. The record does not flag a discrepancy between the posted result and the recalculation. The registry-reported analysis remains the appropriate result to cite as the trial’s own analysis, while the unadjusted recalculation offers a distinct summary of the posted counts.

Neither analysis alone addresses all sources of uncertainty. Their interpretation depends on the endpoint definition, the analysis population, and assumptions used by each method. Further details of the statistical analysis plan are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary efficacy endpoint: the number of participants with gastric ulcer confirmed by endoscopy over 6 months. It also lists secondary outcomes covering other gastrointestinal events and symptom measures. The record does not report how the testing of secondary outcomes was organized, whether a hierarchy was prespecified, or whether multiplicity adjustments were planned or applied. Without those details, secondary p-values should not be interpreted as though they necessarily preserve a single overall false-positive rate across all outcomes.

The primary endpoint description names the ITT Population. The registry record does not provide a full operational definition of that population or details of exclusions and analysis-set membership. It also does not describe how missing endoscopy results, withdrawals, or other incomplete assessments were handled. The completion definition says participants completed the study by performing all scheduled assessments through the 6-month visit or by reaching the gastric-ulcer endpoint; it does not state how missing values were treated in the statistical analysis.

The record does not report an imputation method, a sensitivity analysis for missing data, or assumptions about outcomes for participants without an observed endpoint assessment. Those omissions matter because conclusions can depend on how incomplete outcomes are handled, especially if missingness differs between arms or is related to ulcer occurrence. No such difference or mechanism can be inferred from the registry information.

Other details that would clarify the statistical plan are not reported in the registry record, including the original sample-size justification, interim analyses, exact randomization procedures, and detailed analysis specifications for the reported Cochran-Mantel-Haenszel result. The listed primary analysis population and endpoint are useful, but they do not provide a complete account of the protocol or statistical analysis plan. These gaps limit independent reconstruction and make it important to distinguish the reported primary result from exploratory interpretation of the other outcomes.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: atrial flutter (0.5%), palpitations (0.5%), post-procedural hemorrhage (0.5%), concussion (0.5%), fracture (0.5%).

The registry lists serious adverse events among 5 of 210 participants in the PN400 group and 7 of 210 participants in the naproxen group. It also lists other adverse-event counts of 160 and 174, respectively. These are descriptive counts in the posted record; they do not by themselves establish that an event was caused by a study treatment or provide a comparison adjusted for differences among participants.

The serious-event terms listed include atrial flutter, palpitations, post-procedural hemorrhage, concussion, fracture, and upper limb fracture, each reported as 0.5%. The record does not associate these listed terms with a specific arm in the information available for this summary, so no arm-specific attribution is made. Deaths are not reported in the registry record.

Adverse-event counts should be interpreted alongside the definitions and collection procedures, which are not described in detail in the registry record. The counts do not provide a complete assessment of event timing, severity beyond the serious-event classification, duration, or causal attribution. They should be read as safety reporting, not as evidence that either regimen is safe or unsafe.

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

The primary results describe fewer participants meeting the endoscopically confirmed gastric-ulcer endpoint in the PN400 arm than in the naproxen arm during the 6-month comparison. The registry’s reported analysis gives a value of 11.9, a 95% confidence interval from 7.9 to 17.1, and p = 0.001. The posted arm counts are 15 of 210 and 51 of 210. These findings concern the trial’s defined endpoint and the participants included in its reported analysis.

They do not establish that every participant receiving PN400 would avoid an ulcer, or that every participant receiving naproxen would develop one. They do not determine outcomes beyond the study period, effects in populations not represented by the trial, or the balance of benefits and harms across all possible outcomes. The registry record does not report detailed eligibility criteria, missing-data methods, or the complete analysis plan, which limits broader interpretation.

The trial compared a combination of naproxen and immediate-release esomeprazole with naproxen alone. The result therefore addresses the difference between these assigned regimens in this trial; it does not isolate the contribution of each component or answer questions about other doses or treatment schedules. The primary endpoint is an endoscopic finding, not a comprehensive measure of symptoms or quality of life.

Statistical evidence and clinical meaning are related but distinct. A p-value and confidence interval characterize the data under an analysis method; they do not, by themselves, determine the importance of the result for a person or establish a treatment recommendation. The secondary outcomes and adverse-event reports add context, but their interpretation is limited by differing outcome definitions and the lack of a reported multiplicity plan. The evidence should therefore be understood as a comparison of the posted trial outcomes, not as medical advice or a conclusion about every setting in which these regimens might be used.

18. Why This Trial Matters Statistically

This trial illustrates why endpoint definition matters in clinical statistics. The primary outcome is not a general label such as gastrointestinal harm; it is a participant-level event requiring endoscopic confirmation and specified ulcer features. That definition gives the analysis a clear target, while also limiting what the result can say about symptoms, other lesions, or broader health outcomes.

It also demonstrates the importance of keeping statistical summaries distinct. The registry reports a Cochran-Mantel-Haenszel analysis, while a recalculation from the posted counts is unadjusted. Both can help describe the comparison, but they do not necessarily use the same method or scale. Readers should not treat an unadjusted check as a replacement for the trial’s reported analysis, nor assume that two different summaries are interchangeable.

Precision is another central consideration. A confidence interval communicates uncertainty around an estimate, while a p-value addresses compatibility with a null model under stated assumptions. Neither quantity alone establishes clinical importance or protects against bias, missing-data problems, or multiplicity. The registry record does not report several details needed to fully reconstruct those aspects of the analysis.

Finally, the planning illustrations show how the number of participants required depends on the effect a future study aims to detect and the chosen power target. They are not a record of the original design justification and are not evidence about the completed trial’s power. Separating observed results, reported analyses, recalculations, and planning assumptions is essential for a careful reading of clinical trial evidence.

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 details that would help assess the results are not reported in the registry record. These include the eligibility criteria defining elevated ulcer risk, the randomization procedure, the blinding and allocation-concealment procedures, the endoscopy schedule, and whether endoscopic assessments were centrally reviewed or adjudicated. The double-blind, randomized design is stated, but the practical details needed to evaluate its implementation are not available in the record.

The primary analysis population is identified as ITT, but further population definitions and the handling of participants without evaluable endoscopy results are not reported. The record does not describe missing-data methods or sensitivity analyses. It also does not report a full statistical analysis plan, the sample-size justification for the original trial, or whether interim analyses were planned.

The sponsor’s reported primary result is described using the Cochran-Mantel-Haenszel method, but the registry does not identify the strata or provide enough detail to reproduce the analysis. The unadjusted recalculation is a separate summary and cannot answer questions about the full reported analysis. A multiplicity strategy for the secondary outcomes is not reported, which limits confirmatory interpretation of those results.

The study period and primary endpoint timeframe are specified as 6 months, so the record does not establish outcomes beyond that duration. The adverse-event information is also limited: deaths are not reported in the registry record, listed serious-event terms are not linked to a specific arm in the available information, and detailed event definitions or causal assessments are not described. These limitations concern what can be concluded from the registry record and should not be mistaken for evidence that a particular bias or safety issue occurred.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluating PN 400 (VIMOVO) in Reducing Gastric Ulcers Compared to Non-steroidal Antiinflammatory Drug (NSAID) Naproxen — NCT01129011.
• Registry record last updated 2010-12-28; status last verified 2010-11.
• Results first posted 2010-12-28.
• 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.

23. Record Summary

NCT01129011 is a completed phase 3 randomized, double-blind, parallel-group, controlled, multicenter study of PN400 (VIMOVO) and naproxen in participants at risk of NSAID-associated ulcers. Enrollment was 420. PN400 contained naproxen 500 mg and immediate-release esomeprazole 20 mg dosed twice daily; the comparator was naproxen 500 mg twice daily.

The primary endpoint was the number of participants with gastric ulcer confirmed by endoscopy during 6 months. The posted results list 15 events among 210 participants in the PN400 arm and 51 among 210 in the naproxen arm. The registry reports a Cochran-Mantel-Haenszel analysis with value 11.9, a 95% confidence interval from 7.9 to 17.1, and p = 0.001. A separate unadjusted recalculation is not the same analysis.

The registry lists secondary gastrointestinal and symptom outcomes, but does not report a multiplicity plan, detailed missing-data methods, or the original sample-size justification. The record is evidence about the specified comparison and outcomes during the trial period; it does not resolve questions beyond them.