Cobiprostone Prevention of NSAID-induced Gastroduodenal Injury: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Cobiprostone Prevention of NSAID-induced Gastroduodenal Injury (NCT00597818), a randomized phase 2 study. The primary outcome is Number of Participants With Gastric Ulcers.

2. Clinical Question

The registry describes the study’s purpose as evaluating the efficacy and safety of three cobiprostone dose levels compared with placebo in OA/RA participants treated with an NSAID. The clinical question is therefore about whether the posted ulcer counts differ across the randomized groups during the stated follow-up. The counts alone do not establish why any difference arose, and the comparisons do not isolate an effect from factors not described in the record.

The primary endpoint is one part of a broader set of posted outcomes. Other outcomes address duodenal and gastroduodenal ulcers, combined ulcer categories at Week 4, and ulcer or erosion size at 20 months. Those outcomes can provide context, but they do not replace the prespecified primary question. The registry record does not report a protocol rationale for choosing this endpoint or for the 20-month assessment time.

3. Trial Design

The registry record describes a randomized, parallel-group, phase 2 study with placebo control and quadruple masking. Its official title calls it double-blinded, while the structured masking description says quadruple; the record does not explain that difference. Enrollment was 121. The study status is completed, with a start recorded as 2007-08 and primary completion as 2009-04. The sponsor is Sucampo Pharma Americas, LLC.

Participants were allocated to matching placebo or one of three cobiprostone schedules: 18 mcg once daily, 18 mcg twice daily, or 18 mcg three times daily. The arm descriptions specify 20 months of assigned treatment. NSAID treatment is part of the study population description, which identifies participants with osteoarthritis and/or rheumatoid arthritis receiving an NSAID. The registry record does not describe a particular NSAID regimen, rules for changing background treatment, or how adherence to assigned treatment was assessed.

The primary outcome was the number of participants with gastric ulcers at 20 months. Its population is described as the intention-to-treat population, defined in the record as all participants enrolled. The posted arm counts are 7 of 30 for placebo, 5 of 30 for once-daily cobiprostone, 7 of 31 for twice-daily cobiprostone, and 4 of 30 for three-times-daily cobiprostone. The registry record does not report how missing endpoint observations were handled or whether participants who stopped assigned treatment remained in the endpoint assessment.

Secondary outcomes cover participants with duodenal and gastroduodenal ulcers at 20 months; participants with gastric, duodenal, and gastroduodenal ulcers at Week 4; and ulcer or erosion size at 20 months. These add outcomes at different times and with different definitions, so they should not be treated as interchangeable measures of the primary endpoint. The original sample-size rationale and the trial’s own detailed statistical analysis plan 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.

Before assignment: Of 124 participants recruited, only 121 were actually enrolled.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intention to treat (ITT) population, defined as all participants enrolled in the trial

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.

Population: All subjects recruited were included in the baseline analysis set. Of the 124 participants recruited, only 121 were actually enrolled.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Gastric Ulcers, measured over at 20 months.

The primary endpoint counts participants with gastric ulcers at 20 months. It is a binary outcome at the participant level: each participant either contributes to the count as having a gastric ulcer or does not. The registry identifies the outcome unit as participants and says the analysis population includes all participants enrolled in the trial.

A count of affected participants is useful for expressing how often the outcome occurred in each randomized group. It is directly interpretable as the number of participants with the event among those assessed, though the counts should be read alongside each group’s denominator. Here, the posted denominators are 30 for placebo, 30 for once-daily cobiprostone, 31 for twice-daily cobiprostone, and 30 for three-times-daily cobiprostone.

The primary measure is specifically gastric ulcers. It does not combine gastric ulcers with duodenal or gastroduodenal ulcers, and it does not describe ulcer size or erosion size. Those are separate posted outcomes. The registry record does not report a rationale explaining the choice of gastric ulcers as the primary endpoint, the method used to ascertain ulcers, or whether endpoint assessment was centrally reviewed. In general, a defined endpoint helps focus the main comparison and limits the risk of treating whichever result appears most favorable as the central finding.

The reported endpoint time is 20 months. The record does not provide further details about the assessment window, handling of participants with incomplete follow-up, or how a participant with multiple ulcers was counted. The results should therefore be read as the posted participant counts at the stated time, not as a measure of ulcer episodes or total lesions.

7. Results Posted in the Registry

• Cobiprostone QD: 16.7% (5/30) versus 23.3% (7/30) on control; risk difference -6.7 percentage points (95% CI -26.8 to 13.5), risk ratio 0.71 (0.25–2.00); unadjusted two-proportion z-test p = 0.519.
• Cobiprostone BID: 22.6% (7/31) versus 23.3% (7/30) on control; risk difference -0.8 percentage points (95% CI -21.9 to 20.4), risk ratio 0.97 (0.39–2.43); unadjusted two-proportion z-test p = 0.944.
• Cobiprostone TID: 13.3% (4/30) versus 23.3% (7/30) on control; risk difference -10.0 percentage points (95% CI -29.4 to 9.4), risk ratio 0.57 (0.19–1.75); unadjusted two-proportion z-test p = 0.317.

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.

Number of Participants With Duodenal and Gastroduodenal Ulcers

• 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:
  • Cobiprostone QD: 13.3% (4/30) versus 3.3% (1/30) on control; risk difference 10.0 percentage points (95% CI -3.8 to 23.8), risk ratio 4.00 (0.47–33.73); unadjusted two-proportion z-test p = 0.161.
  • Cobiprostone BID: 3.2% (1/31) versus 3.3% (1/30) on control; risk difference -0.1 percentage points (95% CI -9.0 to 8.8), risk ratio 0.97 (0.06–14.78); unadjusted two-proportion z-test p = 0.981.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cobiprostone QD and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cobiprostone BID and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Gastric, Duodenal, and Gastroduodenal Ulcers

• 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:
  • Cobiprostone QD: 26.7% (8/30) versus 23.3% (7/30) on control; risk difference 3.3 percentage points (95% CI -18.6 to 25.2), risk ratio 1.14 (0.47–2.75); unadjusted two-proportion z-test p = 0.766.
  • Cobiprostone BID: 25.8% (8/31) versus 23.3% (7/30) on control; risk difference 2.5 percentage points (95% CI -19.1 to 24.1), risk ratio 1.11 (0.46–2.67); unadjusted two-proportion z-test p = 0.823.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cobiprostone QD and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cobiprostone BID and the control. The interval gives the range of effects that remain compatible with the data.

Size of Ulcers/Erosions

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Cobiprostone QD: mean 4.70 versus 8.50 on control; difference -3.80 (95% CI -11.19 to 3.59), standardized effect d = -0.26; z-test p = 0.314.
  • Cobiprostone BID: mean 3.50 versus 8.50 on control; difference -5.00 (95% CI -12.38 to 2.38), standardized effect d = -0.35; z-test p = 0.184.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cobiprostone QD and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cobiprostone BID and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover distinct aspects of gastroduodenal injury: ulcer categories at 20 months, a combined ulcer outcome at Week 4, and ulcer or erosion size at 20 months. Across these measures, the observed pattern is not uniformly aligned with the primary endpoint. The ulcer-count outcomes do not show a consistent gradient across all cobiprostone schedules, while the group means for ulcer or erosion size move in a direction different from the mixed count patterns. These measures differ in definition and timing, so inconsistency is not unexpected and does not itself resolve the primary comparison.

The secondary findings offer context about outcomes beyond gastric ulcers, but they should not be treated as independent replications of the primary result. A count of participants with a particular ulcer category is not equivalent to a continuous measurement of lesion size. An assessment at Week 4 also addresses a different point in follow-up from the primary endpoint at 20 months. The registry record does not report a rationale for the timing or hierarchy of these secondary outcomes.

The registry record contains no reported secondary analyses. The arm-level summaries and unadjusted comparisons can be described, but the record does not establish that formal confirmatory tests were planned or performed for these outcomes. When many outcomes or contrasts are examined, some differences can appear by chance. In general, multiplicity refers to the increased chance of misleading findings when multiple hypotheses are tested without accounting for the number of tests. The registry record does not report a multiplicity adjustment or a testing hierarchy.

For those reasons, the secondary outcomes carry less evidential weight than a clearly specified primary analysis with a reported statistical plan. They can prompt questions for future research, but they do not settle whether the primary gastric-ulcer contrast is real or clinically important. The uncertainty around the primary endpoint remains central to interpretation.

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

• Number of Participants With Duodenal and Gastroduodenal Ulcers
• Number of Participants With Gastric, Duodenal, and Gastroduodenal Ulcers
• Size of Ulcers/Erosions

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary participant-level endpoint, recorded as the number of participants with gastric ulcers at 20 months. A natural comparison for a binary endpoint is the difference between the event proportions in two groups. The posted risk difference is expressed as the cobiprostone group’s proportion minus the placebo group’s proportion. A negative estimate means the observed proportion was lower in the cobiprostone group; a positive estimate means it was higher. This is a descriptive direction, not a causal conclusion by itself.

What the confidence interval conveys

A confidence interval describes uncertainty around an estimated contrast under the assumptions of the method used. It gives a range of values that are reasonably compatible with the observed data and the calculation. When an interval for a risk difference includes zero, the data do not rule out no difference at the confidence level used. The primary endpoint intervals all include zero and extend in both directions, so they also allow for differences favoring either group. An interval is not a probability statement that the true value lies within its endpoints, and it does not account automatically for sources of bias or unreported analysis choices.

Width matters as much as the central estimate. A narrow interval would indicate more precise estimation, while a wide interval allows a broader range of plausible contrasts. The primary intervals are wide relative to their central estimates. That is consistent with the small posted group sizes and limited event counts, though the interval calculation itself depends on statistical assumptions. The registry record does not report the sponsor’s method for estimating uncertainty or a detailed analysis plan.

How to read the p-values

The unadjusted p-values summarize how compatible the observed data are with a null comparison under the particular test assumptions. They are not the probability that the null hypothesis is true, nor do they measure the size or clinical importance of a difference. Larger p-values do not demonstrate equivalence. The p-values posted for the primary contrasts are not small, and the confidence intervals include zero; together, these indicate that the data do not precisely distinguish the observed differences from no difference. Since the registry record does not report adjustment for multiple comparisons, these p-values should be viewed as unadjusted.

In general, random allocation is intended to make treatment groups comparable on average, reducing confounding by measured and unmeasured baseline factors. It does not guarantee perfect balance in a small trial. Masking can reduce the influence of knowledge of treatment assignment on care or outcome assessment, but the registry record does not describe who was masked or how endpoint assessment was conducted. The structured record reports quadruple masking, while the official title describes the study as double-blinded; the relationship between those descriptions is not reported in the registry record.

Why outcome definition and population matter

The primary endpoint counts participants, not individual ulcer lesions. Its definition is restricted to gastric ulcers at 20 months, whereas the secondary outcomes cover other ulcer categories, an earlier assessment, and lesion size. Results across such outcomes need not match because they measure different things and may be observed at different times. The stated intention-to-treat population includes all enrolled participants, an approach that aims to preserve the randomized comparison. However, the registry record does not report the number with missing endpoint observations, how missing values were treated, or whether every enrolled participant contributed an observed endpoint.

The posted comparisons are unadjusted. The record does not report whether any covariates were included in the trial’s own analysis, whether there were interim analyses, or whether any analysis populations other than the described intention-to-treat population were used. Those details are not reported in the registry record and should not be inferred from the arm counts.

Reading the secondary continuous measure

Ulcer or erosion size is reported as a mean with a standard deviation. A mean describes the group’s average measurement, while the standard deviation describes the spread of measurements around that average. The posted placebo standard deviation is 20.49 mm, compared with 2.63 mm, 2.35 mm, and 1.54 mm across the cobiprostone groups. In general, large differences in spread can make a simple comparison of means sensitive to distributional assumptions and to a small number of unusually large observations. The registry record does not report whether the measurement distribution was checked, transformed, or analyzed with a method that accounts for unequal variability.

More broadly, statistical estimates rely on assumptions about sampling, endpoint measurement, and the analysis method. The displayed unadjusted summaries are useful for seeing the magnitude and uncertainty of group contrasts, but they cannot resolve missing design details. The registry record does not report the original sample-size justification, the full statistical analysis plan, interim monitoring, or multiplicity procedures. In general, these details matter because they clarify which comparisons were primary, how uncertainty was quantified, and how results were selected for emphasis.

11. Confidence Intervals and Precision

The risk-difference intervals for the primary endpoint are -0.268 to 0.135 for once-daily cobiprostone versus placebo, -0.219 to 0.204 for twice-daily dosing, and -0.294 to 0.094 for three-times-daily dosing. Each interval includes zero and spans values on both sides of zero. The estimates therefore have limited precision: they do not pin down the direction or size of the underlying difference narrowly.

For the once-daily comparison, the central estimate is -0.067; the interval is compatible with a lower event proportion in the cobiprostone group, no difference, or a higher event proportion. The twice-daily estimate is -0.007, with an interval that also permits differences in either direction. The three-times-daily estimate is -0.1, but its interval likewise includes zero and extends to a positive value. The interval endpoints are not predictions of the results a future trial must produce.

In general, confidence intervals are especially important when group sizes and event counts are limited. The observed counts can look different while still leaving considerable uncertainty about the underlying contrast. A confidence interval does not capture every uncertainty: it cannot correct for bias in endpoint assessment, missing outcomes, or unreported analytic decisions. The registry record does not report missing-data handling or the statistical method used by the trial’s own analysis. Those omissions constrain interpretation beyond the uncertainty represented in the posted intervals.

The posted intervals should be read as estimates of precision, not as a verdict about whether a meaningful effect exists. They leave room for a range of effects, and the trial’s observed data do not provide a narrow estimate for any of the primary comparisons.

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 illustrative sample sizes based on the observed group contrasts, not a record of the original trial’s design calculations. For the binary endpoints, the figures are participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses the stated fraction of the observed effect as the effect to detect. The original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were present. The 90% power column uses a higher target chance of detection and therefore generally requires more participants. These are planning targets, not guarantees. They depend on the assumed effect size and analysis conditions.

Rows that plan for 75% or 50% of the observed effect assume a smaller difference than the full observed estimate. Smaller effects are harder to distinguish from random variation, so the calculations require more participants per arm. This pattern is particularly pronounced when the observed difference is close to zero; for the twice-daily primary comparison, the listed planning requirements are very large. That reflects the calculation’s dependence on the small observed contrast, not evidence that a future study must enroll those exact numbers.

These figures are not observed power. Observed power would not add useful information about the uncertainty in the completed data; the confidence intervals convey that uncertainty more directly. The planning calculations also do not account for unreported features such as missing data, multiplicity, or the trial’s actual analysis plan. They are illustrations for future planning under stated assumptions, rather than a retrospective assessment of whether the completed trial was adequately designed.

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 = 0.233; treatment proportion p₁ = 0.167; average p̄ = 0.200.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5657 = 1.1087.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5637 = 0.4744.
4. n = (1.1087 + 0.4744)² / (-0.0667)² = 563.9, rounded up to 564 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 <- 0.233333333333333                          # control proportion
p1 <- 0.166666666666667                          # 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(597818)
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 = 564 (80% power), 755 (90% power)
 75% of observed effect: n per arm = 1,035 (80% power), 1,385 (90% power)
 50% of observed effect: n per arm = 2,397 (80% power), 3,208 (90% power)
power.prop.test: 563.9 
Simulated power at n = 564 per arm: 0.804 (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. Multiplicity, Missing Data and Analysis Populations

The registry record identifies the primary endpoint and lists secondary outcomes, but a detailed statistical analysis plan is not reported in the registry record. It does not state how the several treatment comparisons were prioritized, whether a hierarchy of hypotheses was used, or whether any adjustment for multiple comparisons was planned. This matters because examining multiple doses and multiple outcomes can increase the chance that at least one result appears notable through random variation alone. The posted p-values are unadjusted and should be interpreted accordingly.

Missing-data procedures are also not reported in the registry record. The primary endpoint is described for an intention-to-treat population defined as all participants enrolled, but the record does not state how many participants had unavailable outcome information, how missing values were handled, or whether any sensitivity analyses were performed. An intention-to-treat definition supports retaining participants in their randomized groups, but it does not by itself specify how unobserved outcomes are represented in an analysis.

The registry record does not report whether interim analyses were planned or conducted, whether there was a data-monitoring process, or whether stopping rules were specified. It also does not report a detailed analysis population beyond the stated primary population, or how deviations from assigned treatment were handled. These details should not be inferred from the posted group counts or from the study’s completed status.

These gaps do not invalidate the observed counts, but they limit assessment of how the trial’s own investigators analyzed the data and how complete the endpoint information was. The posted comparisons are unadjusted summaries and do not replace a full protocol or statistical analysis plan. In general, transparent reporting of analysis populations, missing-data handling, interim monitoring, and multiplicity procedures helps readers judge how robustly results answer the primary question.

15. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: diarrhoea (40.0%), dyspepsia (20.0%), erosive oesophagitis (20.0%), nausea (16.7%), gastritis (16.7%).

The posted serious-adverse-event figures give the number affected and the number at risk in each group: placebo, 22 of 30; once-daily cobiprostone, 23 of 30; twice-daily cobiprostone, 25 of 31; and three-times-daily cobiprostone, 26 of 30. These figures describe participants affected in each group, not a comparison adjusted for follow-up or other factors. The registry record does not provide a comparative statistical analysis of these safety counts.

The record lists Diarrhoea (40.0%), Dyspepsia (20.0%), Erosive oesophagitis (20.0%), Nausea (16.7%), Gastritis (16.7%), and Flatulence (13.3%). The record does not clarify the denominator or the precise basis for these listed percentages. Deaths are not reported in the registry record. Counts of affected participants do not show event severity, duration, causality, or whether one participant experienced more than one event. These data should be read as descriptive safety reporting, not as proof of a difference between groups.

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

The posted primary results show that the number of participants with gastric ulcers at 20 months was lower in the once-daily and three-times-daily cobiprostone groups than in the placebo group, while the twice-daily group had the same event count as placebo. The corresponding risk-difference estimates are negative for the once-daily and three-times-daily comparisons and close to zero for twice-daily dosing. The confidence intervals are wide and include zero for all three comparisons. The data therefore do not provide a precise estimate of the difference between any cobiprostone schedule and placebo.

These findings do not establish that cobiprostone prevents gastric ulcers, nor do they establish that it has no effect. A non-small unadjusted p-value does not prove equivalence or rule out a meaningful effect. Conversely, a lower observed count in a treatment group is not by itself proof of benefit. The interpretation must account for uncertainty, the small group sizes, the endpoint definition, and the limitations in registry reporting.

The results apply to the population and treatment context described in the record: participants with osteoarthritis and/or rheumatoid arthritis receiving an NSAID, assigned to one of the posted cobiprostone schedules or placebo. The registry record does not report enough detail to determine how broadly these observations generalize to other populations, NSAID regimens, or durations.

The secondary findings measure different ulcer categories, timing, and lesion size. They provide additional descriptive information, but their analyses are not reported and multiplicity handling is not described. They should not be used to select a favorable result while disregarding the uncertainty in the primary comparison. The posted safety counts are likewise descriptive; they do not establish comparative risk or causality.

Overall, the record documents a completed randomized phase 2 study and arm-level outcomes, but it does not provide a full analysis plan or key details about missing data and endpoint assessment. The results can inform statistical discussion of observed counts and precision, but they are not a stand-alone basis for claims about treatment efficacy or safety.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between an observed group contrast and a precise estimate of an underlying effect. The primary counts vary across randomized groups, but the intervals remain broad and include no difference. Reading only the central estimates would obscure how much uncertainty remains. Reading only the p-values would also miss the range of effects compatible with the data.

The record also shows why the scale and definition of an endpoint matter. The primary outcome is a count of participants with gastric ulcers, while other outcomes use different ulcer categories, a different assessment time, or a continuous measure of lesion size. These outcomes address related but non-identical questions. A pattern across them cannot be reduced to a single treatment effect without an explicit analysis plan.

Planning calculations based on observed effects highlight another statistical issue: estimates from small studies can be unstable. When the observed effect is modest, planning for that effect can imply very large sample requirements; the required size also grows when planning for a smaller effect. Such calculations are useful illustrations, but they are not evidence that the completed study had a particular power or that a future study should adopt those exact targets.

Finally, the record leaves key analysis details unreported, including missing-data handling and multiplicity procedures. These omissions matter for evaluating how confidently the results answer the primary question. Together, the endpoint counts, uncertainty intervals, secondary outcomes, and reporting gaps make this a useful example of why clinical trial interpretation depends on more than whether one observed group had fewer events than another.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The arm sizes are limited, and the primary outcome counts are small. This makes the observed contrasts sensitive to a small number of participants and is reflected in the wide confidence intervals. The trial record does not report a sample-size justification or the assumptions used in the original design, so the intended precision or target effect cannot be assessed from the registry entry.

The registry record does not describe how gastric ulcers were ascertained, the assessment window around 20 months, or how multiple lesions in one participant were counted. It also does not report the amount of missing endpoint data or the method used to handle missing observations. These omissions make it difficult to assess outcome measurement and completeness.

The posted comparisons are unadjusted. The record does not report adjustment for multiple comparisons despite the presence of several treatment contrasts and secondary outcomes. Nor does it provide a detailed statistical analysis plan, interim-analysis information, or sensitivity analyses. These limits leave uncertainty about which analyses were planned and how robust the results are to analytic choices.

There is a reporting discrepancy between the official title’s description as double-blinded and the structured masking description of quadruple masking; the registry record does not explain it. Details of who was masked are not reported. The registry also does not provide details about the NSAID regimens, adherence, treatment discontinuation, or handling of deviations from assigned treatment. These factors may affect interpretation, but their influence cannot be determined from the record.

Generalizability is also constrained by the specific population and treatment context recorded: participants with osteoarthritis and/or rheumatoid arthritis receiving an NSAID. The registry record does not supply enough information about participant characteristics or clinical settings to judge how these results may apply elsewhere. These limitations call for cautious interpretation rather than a categorical conclusion.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Cobiprostone Prevention of NSAID-induced Gastroduodenal Injury — NCT00597818.
• Registry record last updated 2019-12-26; status last verified 2018-03.
• Results first posted 2019-12-26.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT00597818 is a completed randomized, parallel-group, phase 2, placebo-controlled trial of cobiprostone for prevention of NSAID-induced gastroduodenal injury in participants with osteoarthritis and/or rheumatoid arthritis. The registry reports quadruple masking, enrollment of 121, a study start of 2007-08, and primary completion in 2009-04. Assigned treatments were placebo or cobiprostone 18 mcg once daily, twice daily, or three times daily, described for 20 months.

The primary endpoint was the number of participants with gastric ulcers at 20 months in an intention-to-treat population defined as all enrolled participants. The posted counts were 7 of 30 for placebo, 5 of 30 for once-daily dosing, 7 of 31 for twice-daily dosing, and 4 of 30 for three-times-daily dosing. Unadjusted risk-difference intervals include zero for all three comparisons and are wide. Secondary outcomes address other ulcer categories and ulcer or erosion size. The registry record does not report the original sample-size rationale, missing-data procedures, multiplicity handling, or a detailed statistical analysis plan.