Nexium (Esomeprazole) in Symptom Adapted Therapy in GERD Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Nexium (Esomeprazole) in Symptom Adapted Therapy in GERD Patients (NCT00444275), a randomized phase 4 study. The primary outcome is Efficacy of Three Strategies of Long-term Treatment.

2. Clinical Question

3. Trial Design

The registry describes a randomized, open-label, parallel-group, phase 4 study. Its official title identifies an initial 4-weeks acute treatment phase followed by a 12 weeks maintenance phase. The primary outcome timeframe is stated as 16 weeks, and the outcome description locates the maintenance assessment between V2 at 4 weeks and V3 at 16 weeks. The study status is completed; the registry lists enrollment as 3029.

Three maintenance strategies are represented in the primary results: esomeprazole 20 mg once daily, esomeprazole 20 mg on demand, and antacid treatment. The record also lists initial-phase esomeprazole regimens of 20 mg once daily and 40 mg once daily. The arm descriptions do not give further details about how participants moved from the initial phase into maintenance or how the initial regimens were allocated. Those details are not reported in the registry record.

Open-label means the study was not masked according to the registry. Participants and investigators may therefore have known the assigned strategy; the registry does not describe additional steps to reduce the influence of that knowledge on patient-reported responses. Parallel-group means the strategies were compared across groups rather than by having each participant receive every maintenance strategy. The registry states random allocation but does not report the sequence-generation or allocation-concealment procedures.

The stated purpose was to compare long-term treatment strategies for reflux disease in primary care. The record names AstraZeneca as sponsor and gives the study dates as 2007-03 and 2008-10 for start and primary completion. It does not report the original sample-size assumptions, a detailed statistical analysis plan, or the protocol's prespecified handling of missing outcome data.

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: The study included 2 phases (maximum treatment duration = 16 weeks): * one initial treatment phase of 4 weeks * one randomized maintenance treatment phase of 12 weeks only for patients whose initial treatment is considered to be successful at the end of the initial phase. Only maintenance phase data were reported in the Baseline module measures.

Initial Treatment Phase

Maintenance Treatment Phase

Reasons for not completing this period:

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 Efficacy of Three Strategies of Long-term Treatment, measured over 16 weeks.

The primary endpoint is the percentage of participants classified as having maintenance-treatment failure. It was assessed by the patient between V2 at 4 weeks and V3 at 16 weeks. The criterion combines two questions: whether treatment produced sufficient control of reflux symptoms and whether the participant wished to continue the treatment. A participant was classified as a failure if at least one response was negative.

This is a binary outcome: each assessed participant is classified as either meeting or not meeting the failure definition. Reporting the percentage gives a direct description of how often the defined experience occurred in each strategy group. Comparing these percentages can describe differences in failure frequency between strategies. The endpoint is patient-reported, so it captures the participant's judgment of symptom control and willingness to continue rather than an investigator's symptom assessment alone.

The combined criterion has an important interpretive feature. A negative response to either question is sufficient for failure, so the endpoint does not isolate symptom control from treatment preference. A difference between groups could reflect either component or both. The registry record does not report results for the two questions separately, nor does it state how missing answers to either question were classified.

7. Results Posted in the Registry

• Esomeprazole 20 mg on Demand (Maintenance Phase): 7.8% (67/857) versus 10.6% (92/871) on control; risk difference -2.7 percentage points (95% CI -5.5 to -0.0), risk ratio 0.74 (0.55–1.00); unadjusted two-proportion z-test p = 0.048.
• Antacid Treatment (Maintenance Phase): 43.0% (357/830) versus 10.6% (92/871) on control; risk difference 32.4 percentage points (95% CI 28.5 to 36.4), risk ratio 4.07 (3.31–5.02); 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.

Difference in Symptom Severity Evaluation Performed by the Investigators, When Symptom Severity is Assessed With and Without Reflux Disease Questionnaire (RDQ).

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Esomeprazole 40 mg Once Daily (Initial Phase): 2.3% (18/778) versus 3.7% (71/1909) on control; risk difference -1.4 percentage points (95% CI -2.8 to -0.1), risk ratio 0.62 (0.37–1.04); unadjusted two-proportion z-test p = 0.065.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Esomeprazole 40 mg Once Daily (Initial Phase) and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering investigator symptom-severity assessment, symptom questionnaires, treatment satisfaction, concomitant low-dose aspirin, anxiety and depression, and adverse events. These measures address different aspects of symptoms, patient experience, concomitant treatment, and safety. They are not interchangeable with the primary patient-defined maintenance-failure outcome, which combines symptom control and willingness to continue treatment.

The record contains a posted comparison for investigator-assessed symptom severity at 4 weeks, but it does not give a complete set of reported results across all listed secondary outcomes. The registry describes eight secondary outcomes as posted; it does not provide a corresponding reported analysis for each one. A broad pattern across the secondary endpoints therefore cannot be established from the registry record. Missing or unreported secondary results should not be treated as showing no effect.

Secondary outcomes can help contextualize a primary result when their definitions and timing provide complementary information. For example, an investigator assessment may differ from a patient's combined judgment, and satisfaction or questionnaire measures may capture other dimensions of experience. However, the available record does not establish whether the secondary findings corroborate, explain, or conflict with the primary comparison as a whole.

Unadjusted secondary results carry less weight because examining multiple outcomes and comparisons creates more opportunities for apparently notable results to arise by chance. The registry does not report a multiplicity strategy, a hierarchy among secondary outcomes, or a complete analysis plan. The secondary results are therefore best treated as supportive or exploratory descriptions, rather than independent confirmation of the primary result.

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

• Difference in Symptom Severity Evaluation Performed by the Investigators, When Symptom Severity is Assessed With and Without Reflux Disease Questionnaire (RDQ).
• Impact of Treatment With Low Dose Aspirin (Acetyl Salicylic Acid) Used Concomitantly During the Initial Phase and the Maintenance Phase
• Differences Among Strategies of Maintenance Treatment for Satisfaction of the Patient, Using the GIS (Gord Impact Scale) Scale.(Change in Values of Score Derived From the GIS Questionnaire From V2 to V3 = Start to End of the Maintenance Phase)
• Impact of Anxiety and Depression During the Initial Visit Measured by the HADS ( Hospital Anxiety and Depression Scale) Questionnaire on Response to Initial Treatment and to Maintenance Treatment
• Number of Participants and Type of Serious Adverse Events and Adverse Events Leading to a Premature Discontinuation of the Study
• Score Abacuses Based on the Reflux Disease Questionnaire (RDQ) Questionnaire
• Score Abacuses Based on the Reflux Disease Questionnaire (RDQ) Questionnaire
• Score Abacuses Based on the Reflux Disease Questionnaire (RDQ)

9. Statistical Interpretation

10. Statistical Methods Explained

What does a risk difference describe?

For a binary endpoint, a risk difference expresses the difference between the event proportions in two groups. In this study the event is the defined treatment failure. A negative estimate for on-demand treatment relative to daily treatment indicates a lower observed failure proportion in the on-demand group; a positive estimate for antacid treatment relative to daily treatment indicates a higher observed proportion in the antacid group. The estimate is on an absolute scale, rather than a relative scale such as a risk ratio.

The posted arm percentages are rounded summaries. The comparison statistics use the posted group counts and denominators. Small apparent differences between a rounded arm percentage and a comparison estimate can occur because the underlying calculation uses more detail than the rounded display. The record does not identify a sponsor-reported model for these comparisons. The posted p-values are described as unadjusted, and the record lists no reported analyses.

How should a confidence interval be read?

In general, a confidence interval gives a range of values compatible with the data and the statistical method used, while conveying uncertainty around an estimate. It is not a guarantee that the true value lies within the particular interval, nor does it describe the spread of individual participant outcomes. For a risk difference, zero represents no difference between the group proportions. An interval that excludes zero is conventionally consistent with a difference at the corresponding nominal confidence level; an interval that includes zero is compatible with no difference as well as values on either side.

For the on-demand comparison, the posted interval is close to zero but lies on the negative side. For the antacid comparison, the posted interval is on the positive side. These interval statements concern the unadjusted risk-difference comparisons. They do not account for any multiplicity across comparisons or outcomes, and the registry does not report a broader analysis that would do so.

What does a p-value add?

In general, a p-value measures how surprising data at least as incompatible with a specified null hypothesis would be if that hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. A p-value should be considered with the effect estimate, its interval, the outcome definition, and the analysis plan. The posted values are unadjusted, so they should not be interpreted as controlling the chance of false-positive findings across all comparisons.

Why does the binary endpoint matter?

The primary outcome reduces two patient responses to a single failure classification: at least one negative response means failure. This makes group proportions and risk differences natural summaries. It also compresses information. A participant with one negative response and a participant with two negative responses both satisfy the same failure definition. The registry does not report separate results for the two questions or a score that retains their individual response levels.

What can be said about adjustment and analysis populations?

The record presents group counts and unadjusted comparisons. It does not report covariate-adjusted estimates, a prespecified analysis population, or the handling of missing endpoint responses in the primary analysis. Random allocation is reported, but the available record does not show whether all randomized participants were included in each analysis or whether any exclusions were made. These omissions limit assessment of whether the posted comparisons follow the trial's intended analysis plan.

What is the role of the planning calculations?

General sample-size planning uses assumptions about the event frequency, the effect to detect, the significance level, power, allocation, and statistical method. The planning illustration in the record uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. It considers specified fractions of the observed effect. These are planning assumptions for an illustration, not evidence that the trial was designed or analyzed using those assumptions. The registry record does not report the original trial's sample-size justification or design assumptions.

For binary outcomes, the event proportions influence the number of participants needed to detect a given absolute difference. In general, smaller target effects require more information to distinguish them from random variation. Planning figures are conditional on the assumptions used and should not be read as a guarantee that a future study will reproduce the observed effect. The posted calculations are not a replacement for the trial's original protocol or a formal analysis plan.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a group difference, not whether the difference is important to patients. The registry reports confidence intervals for the two primary comparisons. For the on-demand comparison, the interval lies just below zero, so the posted data are compatible with a small negative difference as well as a larger negative difference within that interval. Its proximity to zero indicates limited separation from the no-difference value. The unadjusted p-value is 0.048.

For the antacid comparison, the interval lies above zero and is separated from zero. Its lower and upper bounds both support a positive difference on the risk-difference scale under the stated unadjusted calculation. The interval is more distant from zero than the on-demand interval, consistent with the larger separation in the posted group percentages. The unadjusted p-value is <0.001.

Neither interval captures all sources of uncertainty. They reflect sampling uncertainty under the comparison method, but do not address possible bias from missing data, outcome measurement, departures from the intended allocation, or an analysis choice made after seeing results. The registry record does not report whether the interval method was prespecified or whether adjusted intervals were calculated.

The endpoint is patient-reported and combines two responses into one classification. That definition may affect the observed event frequency and the precision of the comparison. The record does not provide separate confidence intervals for the two component questions. The secondary result for investigator-assessed symptom severity also has a posted interval, but it is an unadjusted secondary comparison and does not replace the primary endpoint's uncertainty assessment.

Read each interval alongside its point estimate and the design limitations. An interval that excludes zero is not proof of a clinically important difference, and one close to zero does not establish equivalence. The registry does not report a prespecified equivalence or non-inferiority margin.

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 are not total events. The 80% column gives the planned number per group that, under the listed assumptions, would yield an 80% chance of detecting the target effect if that effect were present. The 90% column expresses the same planning idea with a higher target chance of detection. Greater planned power generally requires more participants when the other assumptions are held fixed.

The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The rows therefore represent planning for 100%, 75%, and 50% of the observed effect. The trial's original design assumptions and sample-size justification are not reported in the registry record, so these figures should not be mistaken for the design basis of the completed study.

Smaller target effects require more participants because they are harder to distinguish from random variation. The planning counts depend on the observed effect used as their starting point, and a future study may have different event rates or other design features. The displayed values are illustrations conditional on the stated assumptions, not a recommendation for a particular study.

This is not observed power. It is a forward-looking planning calculation based on an assumed effect and method; it does not measure the probability that the completed trial's result is true or reproduce the study's original design process.

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 = 0.106; treatment proportion p₁ = 0.078; average p̄ = 0.092.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4086 = 0.8007.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4081 = 0.3435.
4. n = (0.8007 + 0.3435)² / (-0.0274)² = 1,738.0, rounded up to 1,738 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 <- 0.105625717566016                          # control proportion
p1 <- 0.0781796966161027                          # 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(444275)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,738 (80% power), 2,327 (90% power)
 75% of observed effect: n per arm = 3,194 (80% power), 4,276 (90% power)
 50% of observed effect: n per arm = 7,419 (80% power), 9,931 (90% power)
power.prop.test: 1738 
Simulated power at n = 1,738 per arm: 0.802 (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

Multiplicity arises when several outcomes, treatment comparisons, time points, or analysis choices are examined. Even when each individual test uses a conventional significance threshold, the chance of at least one false-positive finding across a family of tests can increase. Methods such as a prespecified hierarchy or statistical adjustment can address that issue, but they affect how results are interpreted and should be chosen in advance.

The registry lists one primary outcome and multiple secondary outcomes, and the primary result includes comparisons of each of two maintenance strategies with the daily esomeprazole control. It does not report whether the trial used a multiplicity adjustment, a hierarchy among these comparisons, or a prespecified strategy for interpreting the secondary outcomes. The unadjusted p-values should therefore be read as nominal results for the individual comparisons, not as evidence that error rates across all analyses were controlled.

Missing-data handling is also important for a patient-reported endpoint. Participants may have missing answers, may not complete follow-up, or may have different amounts of available information. The registry does not report how missing primary responses were treated, whether any imputation was used, or whether sensitivity analyses assessed alternative assumptions. The available record also does not state whether the primary analysis used all randomized participants, participants who completed the relevant assessments, or another analysis population.

The record lists random allocation but does not provide sequence-generation or allocation-concealment details. It also does not describe protocol deviations or exclusions from analyses. These omissions prevent a full appraisal of whether the groups were analyzed according to the intended randomized comparison and how robust the findings are to missingness or analysis choices. The registry record does not report interim analyses, stopping rules, or a detailed statistical analysis plan, so no conclusions about those procedures can be drawn.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: aggravation of intervertebral disc herniation (0.1%), renal colic (0.1%), adenocarcinom a of gastric antrum (0.1%), metrorrhagia (0.1%), erosive antritis (0.1%).

The adverse-event record gives serious-event counts and other adverse-event counts for the listed exposure groups, with the number at risk for each group. For example, the initial-phase esomeprazole 20 mg group lists 8 serious events among 2156 at risk, and the initial-phase 40 mg group lists 2 among 873 at risk. The maintenance groups list 2 serious events among 886 at risk for daily esomeprazole, 3 among 880 at risk for on-demand esomeprazole, and 4 among 851 at risk for antacid treatment.

These are descriptive counts from the registry record. They should be read with their corresponding at-risk groups and treatment phases; they are not a comparison adjusted for exposure duration or participant characteristics. The record also lists other adverse-event counts, but these counts do not establish that a treatment caused an event. The serious-event terms listed include several terms recorded at 0.1% each.

Death values are not reported in the registry record. The registry's adverse-event entries do not provide enough information to assess event timing, relatedness, severity distributions beyond the listed categories, or comparative safety using a prespecified statistical analysis. The counts alone should not be used to conclude that one strategy is safer than another.

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

The primary result describes how often participants met a specific patient-reported failure definition during the maintenance period. In the posted groups, the failure percentage was lower for on-demand esomeprazole than for daily esomeprazole, and higher for antacid treatment than for daily esomeprazole. The unadjusted comparisons show different degrees of statistical separation from zero, with the on-demand comparison close to that boundary and the antacid comparison farther from it.

These findings do not establish that any treatment works or does not work. They describe the recorded group outcomes under this study's endpoint definition. A participant was considered a failure after at least one negative answer about symptom control or wanting to continue treatment. The result cannot distinguish which of those two responses contributed to the group percentages.

The trial was randomized, which supports comparison of assigned groups, but it was open label and the primary outcome relied on participant responses. The registry record does not supply enough information to assess missing data, adherence, analysis populations, or adjustment for multiple comparisons. These factors limit how completely the posted estimates can be interpreted as causal or confirmatory evidence.

The record also does not report a non-inferiority or equivalence margin. A result that is near zero or an interval that is close to zero does not by itself show that strategies are equivalent. Likewise, a small p-value does not measure clinical importance. Judging practical importance would require a prespecified threshold and fuller clinical context, neither of which is reported in the registry record.

The findings apply to the recorded participants, strategies, setting, endpoint, and follow-up described in the registry. The record does not establish how well the results generalize to populations or care settings with different characteristics. It also does not provide a complete account of all secondary outcomes, so those outcomes cannot be used to make broad claims about the consistency of the primary finding.

17. Why This Trial Matters Statistically

This study illustrates why an endpoint's operational definition matters. Treatment failure is not simply a clinical event recorded by an investigator: it is defined by a participant's answers to questions about symptom control and willingness to continue. Combining the responses yields a clear binary measure for comparing group proportions, but it also merges distinct reasons for failure. Statistical interpretation should therefore remain connected to the actual questions that created the outcome.

The results also show the value of reporting absolute comparisons alongside group percentages. A risk difference communicates the scale and direction of the observed separation in event proportions, while its confidence interval communicates uncertainty. The two primary comparisons have notably different positions relative to zero, reminding readers that one trial can produce a close comparison for one strategy and a more separated comparison for another.

At the same time, the registry record illustrates limits of registry-based interpretation. It reports the randomized, open, parallel design and outcome summaries, but lists no reported analyses and does not give the full analysis plan, multiplicity handling, or missing-data methods. Without those details, unadjusted comparisons are informative descriptions but do not provide a complete account of the trial's inferential approach.

Finally, planning calculations derived from an observed effect are distinct from the original trial design and from retrospective claims about power. Their assumptions must be read explicitly, and smaller target effects require more participants. This distinction helps prevent planning illustrations from being mistaken for a justification of the completed trial or a measure of how conclusive its findings are.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves important design and analysis details unreported. It states that allocation was randomized, but does not describe sequence generation or allocation concealment. It identifies the study as open label, without reporting procedures intended to limit the influence of treatment knowledge on the patient-reported primary outcome. The record does not provide the full eligibility criteria or explain how participants entered the maintenance strategies after initial treatment.

The primary outcome combines two questions into one failure classification. Separate results for symptom control and desire to continue are not reported. The record also does not explain the handling of missing responses, treatment discontinuation, or incomplete follow-up, and it does not identify the primary analysis population. These gaps make it difficult to assess the effect of missing outcome information or departures from the planned treatment strategy.

Although several secondary outcomes are listed, the registry does not report a complete set of analyses for them. It also does not describe a prespecified multiplicity approach or provide the full statistical analysis plan. The posted comparisons are unadjusted, and the record lists no reported analyses. Consequently, the displayed estimates should not be assumed to incorporate covariate adjustment or to represent the complete sponsor analysis.

The adverse-event entries are descriptive counts, with no reported deaths, event-relatedness analysis, or comparative safety model. The record gives no basis for evaluating differences in exposure duration or other factors that could affect event counts. Finally, the planning illustration is not the trial's original sample-size justification, which is not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Nexium (Esomeprazole) in Symptom Adapted Therapy in GERD Patients — NCT00444275.
• Registry record last updated 2012-12-11; status last verified 2012-11.
• Results first posted 2012-12-11.
• 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

NCT00444275 is a completed, randomized, open, parallel-group phase 4 study sponsored by AstraZeneca. It enrolled 3029 participants with symptoms thought to be GERD related and compared three maintenance strategies following an initial acute treatment phase. The registry states that the study was intended to compare long-term reflux-disease treatment strategies in primary care.

The primary endpoint was the percentage meeting a patient-defined maintenance-failure criterion between V2 at 4 weeks and V3 at 16 weeks. Posted group percentages were 10.6 for daily esomeprazole, 7.8 for on-demand esomeprazole, and 43.0 for antacid treatment. The registry lists unadjusted comparisons but no reported analyses. It does not report the trial's original sample-size assumptions, detailed analysis plan, multiplicity handling, or missing-data methods. Secondary and safety records provide additional information but do not resolve those limitations.