High Dose Dual Therapy vs Clarithromycin Triple Therapy for Treatment Naive H Pylori Infection in an Urban Population: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for High Dose Dual Therapy vs Clarithromycin Triple Therapy for Treatment Naive H Pylori Infection in an Urban Population (NCT05342532), a randomized phase 4 study. The primary outcome is Number of Participant With Eradication of Disease.

2. Clinical Question

This is a question about an observed clinical outcome: whether eradication was recorded for participants in each randomized group. It is not a question about the speed of eradication, because the primary endpoint is a participant count rather than a time-to-event measure. Nor does the registry record report a separate estimate for subgroups, such as participant characteristics or infection characteristics.

The posted counts were 37 participants with eradication among 58 assigned to High Dose Dual Therapy and 42 among 54 assigned to Standard Triple Therapy. The statistical comparison expresses the difference in the estimated event proportions as a risk difference, with High Dose Dual Therapy contrasted against Standard Triple Therapy. The estimate is negative, while its confidence interval includes values on either side of no difference. That uncertainty matters when interpreting the observed counts: the point estimate alone does not establish that the underlying outcomes differ between regimens.

The trial was randomized and open-label, so the group comparison has a randomized allocation but no masking. The registry record does not report enough detail to assess how outcomes were ascertained, how missing endpoint observations were handled, or which analysis population was used. Those details are relevant to understanding how closely the posted comparison reflects the randomized groups and how robust it is to incomplete observations.

3. Trial Design

The registry describes a phase 4, prospective, randomized, open-label trial with a parallel-group model. It compared High Dose Dual Therapy with Standard Triple Therapy for treatment-naive H. pylori infection in a diverse urban New York City population. Enrollment was 112. The trial is recorded as completed. The sponsor is Icahn School of Medicine at Mount Sinai.

Participants were assigned to one of two concurrent treatment groups. The posted primary outcome counts show 58 participants in the High Dose Dual Therapy group and 54 in the Standard Triple Therapy group. The first regimen consisted of amoxicillin 1 g three times daily and omeprazole 40 mg three times daily for 14 days. The comparator consisted of clarithromycin 500 mg twice daily, omeprazole 40 mg twice daily, and amoxicillin 1g twice daily for 14 days.

Randomization is intended to allocate participants to groups using a chance-based process, which can reduce systematic differences at the start of a trial. It does not guarantee that groups are identical, and the registry record does not describe the sequence-generation or allocation-concealment procedures. Those procedures are not reported in the registry record. The record identifies masking as none, so the trial is open-label; it does not indicate that participants or clinicians were blinded to assigned treatment.

The primary outcome was the number of participants with eradication after treatment, assessed at the end of the study at 6 weeks. The registry also lists two secondary outcomes: the number of participants with protocol-specific adverse events and the number completing at least 90% of all prescribed medications. Numerical results for those secondary outcomes are not reported in the registry record.

The registry lists enrollment and completion information, but a fuller account of recruitment, follow-up, exclusions, and the participant flow through analysis is not reported in the registry record. The protocol’s original sample-size justification, if any, is also not reported in the registry record. Planning illustrations based on the observed effect are separate from the trial’s original design assumptions.

4. Participant Flow and Accounting

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

Overall Study

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 Number of Participant With Eradication of Disease, measured over end of study at 6 weeks.

The primary endpoint is the number of participants with eradication of disease after treatment, measured at the end of the study at 6 weeks. In plain terms, it counts participants who met the trial’s eradication outcome in each group. The posted count was 37 in High Dose Dual Therapy and 42 in Standard Triple Therapy. The corresponding group sizes were 58 and 54.

A binary outcome such as eradication can be summarized as a count and as an event proportion within each group. The registry’s comparison reports a risk difference: the estimated event proportion in High Dose Dual Therapy minus the estimated event proportion in Standard Triple Therapy. A risk difference is expressed on the absolute probability scale. A value of zero represents no difference in the event proportions; a negative estimate means the estimated proportion is lower in the first-named group than in the comparator group.

This endpoint is useful for a randomized comparison because it describes the outcome of interest directly for participants in each assigned group. It is not a measure of how long eradication took, nor does it describe symptom change or another clinical outcome. The registry describes the endpoint as the number of participants with eradication after treatment, but further operational details—such as the specific test or criteria used to determine eradication—are not reported in the registry record.

Interpreting a count requires attention to its group size. The counts alone do not convey the estimated comparison, and the comparison alone does not show how precisely the underlying difference is estimated. The confidence interval and p-value provide additional statistical context, though neither resolves limitations in outcome definitions, follow-up, or missing-data handling.

7. Results Posted in the Registry

• High Dose Dual Therapy: 63.8% (37/58) versus 77.8% (42/54) on control; risk difference -14.0 percentage points (95% CI -30.6 to 2.6), risk ratio 0.82 (0.64–1.04); unadjusted two-proportion z-test p = 0.105.

8. Statistical Interpretation

9. Statistical Methods Explained

A randomized parallel-group trial assigns participants to separate treatment groups and follows the groups concurrently. In general, random allocation is used to reduce the influence of systematic differences in measured and unmeasured participant characteristics. Randomization does not ensure that every characteristic is balanced, especially in a trial of limited size. The registry identifies this study as randomized and parallel, but the specific randomization and allocation-concealment procedures are not reported in the registry record.

The trial is open-label, meaning masking is listed as none. In general, knowledge of assigned treatment can affect participant behavior, clinical management, reporting of symptoms, or outcome assessment, depending on the outcome and how it is measured. The primary endpoint is an eradication count, but the method used to establish eradication and the safeguards for outcome assessment are not reported in the registry record. The record therefore does not permit a detailed assessment of whether awareness of treatment assignment could have influenced measurement.

What does a risk difference describe?

A risk difference is the difference between the event proportions in two groups. For this comparison, the estimate is expressed as High Dose Dual Therapy minus Standard Triple Therapy. A negative value means the estimated event proportion is lower in the first group; a positive value means it is higher. Zero is the null value for a risk difference. This absolute scale gives a direct contrast in proportions, unlike ratio measures, which describe relative rather than absolute differences.

The posted risk difference is -0.140. Its 95% confidence interval runs from -0.306 to 0.026. The interval includes zero, so the estimated data do not rule out no difference under the method used to construct the interval. A confidence interval is not a range in which the observed estimate itself varies. In general, it is a range of values generated by a procedure that, over repeated studies under its assumptions, would cover the true parameter at the stated rate. It expresses uncertainty in the estimate, not the probability that the true value falls inside this particular interval.

How should the p-value be read?

The unadjusted p-value is 0.105. In general, a p-value describes the compatibility of the observed data, or more extreme data, with a specified null model. It does not state the probability that the null hypothesis is true. It also does not quantify clinical relevance, establish causation, or show that the result will replicate. Here, the p-value is unadjusted; the registry record does not report whether the sponsor conducted other analyses or applied any multiplicity procedure.

Different measures can summarize a binary outcome. The reported risk ratio is 0.820, with an interval from 0.645 to 1.043. A risk ratio compares event proportions by division, with one as its null value. The reported odds ratio is 0.503, with an interval from 0.218 to 1.161. An odds ratio compares odds rather than event proportions, also with one as its null value. Both intervals include one. Odds ratios and risk ratios are not interchangeable, and an odds ratio should not be read as an absolute change in probability. The registry record supplies these estimates but does not describe a model or adjustment strategy behind them.

What does “unadjusted” mean?

In general, an unadjusted comparison uses the group outcome summaries without controlling for additional covariates in a statistical model. Such a comparison can be informative for a randomized trial, where randomization is intended to address confounding at assignment. It does not ensure that chance imbalances are absent, and it cannot answer whether a covariate-adjusted analysis would produce a different estimate. No adjusted analysis is reported in the registry record.

The posted endpoint is binary and reported as participant counts. The registry does not describe imputation, exclusions, or how participants without an evaluable endpoint were handled. Nor does it identify whether the primary comparison followed an intention-to-treat, per-protocol, or other analysis population. Those omissions matter because analysis choices can change which participants contribute to an estimate. It is not possible to infer those choices from the reported counts alone.

In general, over-dispersion is a concern when observed variability exceeds what a statistical model assumes. It is particularly relevant to models for counts or clustered observations. The primary outcome is a participant-level binary event, and no dispersion estimate or model-based analysis is reported in the registry record. It would therefore be inappropriate to claim that over-dispersion was assessed or that a particular correction was used. The analysis details needed to evaluate model assumptions are not reported in the registry record.

The displayed recalculated comparisons are simple unadjusted re-calculations from posted summary statistics, rather than a substitute for a sponsor analysis. The discrepancy indicator is false, so no discrepancy is flagged between the posted summary comparison and the recalculation. A recalculation from summary data cannot reconstruct participant-level adjustments, handling of missing observations, or protocol-specific analysis decisions. Where a discrepancy exists, the sponsor’s own analysis takes precedence; no such discrepancy is indicated for this comparison.

Statistical significance is only one component of interpretation. A small p-value would not establish that an effect is important, and a p-value that is not small does not demonstrate equivalence. Equivalence or noninferiority requires a prespecified margin and an analysis designed for that question. Such a margin and a noninferiority or equivalence analysis are not reported in the registry record. General statistical principles should therefore not be mistaken for features of this trial’s protocol.

10. Confidence Intervals and Precision

The primary risk-difference estimate is -0.140, and its 95% confidence interval is -0.306 to 0.026. The estimate is the single point around which the interval is centered by the method used, while the interval conveys uncertainty about the underlying group contrast. The interval is wide enough to include both a negative difference and a positive difference, as well as zero. The direction suggested by the point estimate is therefore not established with precision by the interval.

In general, a confidence interval gives a range of values reasonably compatible with the data under the statistical method and its assumptions. It is not a guarantee that the true value lies within the endpoints, and it is not a direct probability statement about this one interval. Its width is affected by the amount of information in the data, the variability of the outcome, and the construction method. In this trial, the primary outcome is binary and the groups include 58 and 54 participants, respectively.

The relative measures also have intervals that include their null value. The risk ratio is 0.820, with a confidence interval from 0.645 to 1.043. The odds ratio is 0.503, with a confidence interval from 0.218 to 1.161. These intervals illustrate uncertainty on relative scales; they should not be interpreted as absolute percentage-point contrasts. The three estimates describe the comparison on different scales and are not interchangeable.

Precision is distinct from whether a result crosses a conventional threshold for statistical significance. The risk-difference interval includes zero, and the unadjusted p-value is 0.105. Neither fact establishes that the groups are equivalent. A conclusion of equivalence would require a prespecified range of differences considered acceptably small and an analysis designed to assess that range. Such details are not reported in the registry record.

The registry record does not provide enough detail to evaluate every source of uncertainty, including missing-outcome handling, analysis-population definitions, or outcome-assessment procedures. The confidence interval reflects statistical uncertainty under its method, but it cannot account automatically for all potential biases or gaps in reporting. Precision should therefore be read together with the design and reporting limitations.

11. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm for 80% power and participants per arm for 90% power. They are planning illustrations based on the observed effect, not the trial’s original sample-size justification. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for each planning row is the stated fraction of the observed effect.

For planning for 100% of the observed effect, the figures are 165 participants per arm for 80% power and 221 participants per arm for 90% power. For planning for 75% of the observed effect, they are 284 participants per arm for 80% power and 379 participants per arm for 90% power. For planning for 50% of the observed effect, they are 613 participants per arm for 80% power and 820 participants per arm for 90% power.

In general, power is the probability that a study’s statistical test will detect an effect of a specified size under the assumptions used in the calculation. The 80% column describes a planning target with an 80% chance of detecting the assumed effect under those assumptions; the 90% column uses a higher target. These values do not say what the power of this completed trial was after its results were known. This is not observed power.

The planning figures increase as the effect assumed for detection becomes smaller: a smaller effect is harder to distinguish from random variation and generally requires more participants. The values are illustrative, because they use a fraction of the observed effect and depend on the listed assumptions. The original protocol’s sample-size rationale and design assumptions are not reported in the registry record. For time-to-event outcomes, a planning quantity may instead refer to total events; that does not apply to this binary participant-count endpoint.

12. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.778; treatment proportion p₁ = 0.638; average p̄ = 0.708.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6431 = 1.2605.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6355 = 0.5348.
4. n = (1.2605 + 0.5348)² / (-0.1398)² = 164.8, rounded up to 165 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 <- 0.777777777777778                          # control proportion
p1 <- 0.637931034482759                          # 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(5342532)
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 = 165 (80% power), 221 (90% power)
 75% of observed effect: n per arm = 284 (80% power), 379 (90% power)
 50% of observed effect: n per arm = 613 (80% power), 820 (90% power)
power.prop.test: 164.8 
Simulated power at n = 165 per arm: 0.803 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and two secondary outcomes: the number of participants with protocol-specific adverse events and the number completing at least 90% of all prescribed medications. The record reports three outcome measures, but numerical results for those secondary outcomes are not reported in the registry record. It lists zero analyses. The analysis plan, including any prespecified hierarchy or multiplicity adjustment, is not reported in the registry record.

Multiplicity arises when several outcomes, comparisons, time points, or subgroup analyses are tested. In general, conducting many tests can increase the chance of obtaining at least one apparently unusual result by chance. A prespecified testing order or adjustment can address some multiplicity concerns, but the registry record does not say whether either was planned or used. The reported primary comparison is described as unadjusted, and no additional multiplicity procedure is reported.

Missing-data handling is also not reported in the registry record. The posted primary counts include 58 participants in High Dose Dual Therapy and 54 in Standard Triple Therapy, but the record does not explain whether these are all randomized participants with outcome data, whether any participants lacked endpoint assessments, or how missing outcomes were treated. It does not report imputation or sensitivity analyses.

The analysis population is not reported in the registry record. In general, an intention-to-treat analysis includes participants according to randomized assignment, while per-protocol analyses may apply eligibility or adherence criteria. These approaches answer related but not identical questions and can be affected differently by departures from assigned treatment or missing outcomes. The registry record does not identify which approach was used for the posted primary comparison.

These omissions do not establish that a particular method was or was not used; they mean the method is not documented in the registry record. Without the analysis plan, participant flow, missingness details, and definitions of analysis populations, readers cannot fully evaluate selective reporting or the sensitivity of the comparison to analysis choices.

14. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The posted serious adverse event counts are zero in both groups. The registry lists 58 participants at risk in High Dose Dual Therapy and 54 at risk in Standard Triple Therapy for serious adverse events. No deaths are recorded in either group. The registry lists no serious-event terms.

For other adverse events, the posted counts are 5 among 58 participants at risk in High Dose Dual Therapy and 20 among 54 at risk in Standard Triple Therapy. These are participant counts, not a detailed description of event types, severity, timing, or relationship to treatment. The registry’s secondary outcome description refers to protocol-specific adverse events, but the posted safety summary does not provide a full narrative of those events.

A count of zero recorded serious events does not prove that the risk of serious events is absent. In general, safety counts need to be interpreted in light of the number of people observed, the duration and completeness of follow-up, and how events were collected and classified. Those further details are not reported in the registry record. The listed counts should be read as the safety information recorded for this trial, not as a complete estimate of safety in other settings or populations.

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

The posted primary outcome counts favor Standard Triple Therapy numerically: 42 participants had eradication in that group, compared with 37 in High Dose Dual Therapy. The estimated risk difference for High Dose Dual Therapy relative to Standard Triple Therapy was -0.140. The 95% confidence interval, -0.306 to 0.026, includes zero, and the unadjusted p-value was 0.105. The results therefore leave uncertainty about the size and direction of the underlying difference.

These findings do not establish that either regimen is superior, equivalent, or ineffective. The point estimate describes the observed comparison, while the interval indicates that a range of underlying differences remains compatible with the data under the analysis method. A result that does not meet a conventional significance threshold is not proof of no effect. Likewise, a numerical difference between observed counts is not on its own evidence of a reliable population-level difference.

The comparison also cannot establish that the same results would occur in other populations or care settings. The registry characterizes the study as involving a diverse urban New York City population, but detailed participant characteristics and subgroup results are not reported in the registry record. Generalizability should not be inferred beyond the context documented for the trial.

The registry does not report the method used to confirm eradication, the handling of missing endpoint data, or the analysis population. It also does not report numerical results for the listed secondary adherence and adverse-event outcomes. Those gaps constrain interpretation of both the primary comparison and the broader balance of outcome information.

The safety record lists no serious adverse events and no deaths in either group, with other adverse-event counts of 5 and 20 in the respective groups. These figures are descriptive and do not, by themselves, establish comparative safety. Taken together, the registry record supports a careful description of the observed counts and their uncertainty, rather than a definitive treatment recommendation.

16. Why This Trial Matters Statistically

This trial is statistically informative because it compares two treatment strategies using random allocation and a direct binary endpoint. A participant-level eradication outcome is readily interpretable as a count in each group, and a risk difference expresses the absolute contrast between those group outcomes. Reporting more than one scale—the risk difference, risk ratio, and odds ratio—also illustrates why the choice of effect measure matters when communicating binary results.

The record highlights the difference between an observed point estimate and a precise conclusion. The risk-difference estimate is negative, but its confidence interval extends across zero. The unadjusted p-value is 0.105. Considering the estimate, interval, and test together discourages over-reading the direction suggested by the counts alone. This is a general lesson in trial interpretation: a point estimate is not a certainty, and a p-value is not a measure of the importance of an effect.

The planning illustrations also make visible how sample-size requirements depend on the effect targeted for detection. Their figures rise as the assumed effect becomes smaller, under the stated planning assumptions. Because the calculations are based on the observed effect rather than the trial’s original design, they should be understood as illustrations of planning principles, not as evidence that the original study was designed around those numbers.

Finally, the record shows why reporting detail is part of statistical interpretation. Randomization and group counts are documented, while analysis populations, missing-data methods, outcome-assessment details, and the original sample-size rationale are not reported in the registry record. These omissions limit how fully readers can assess bias, robustness, and the scope of the conclusions. Statistical interpretation depends not only on the numerical result but also on knowing how the result was obtained.

17. Limitations

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

The primary estimate is based on 58 participants assigned to High Dose Dual Therapy and 54 assigned to Standard Triple Therapy. The confidence interval for the risk difference is broad and includes zero, so the estimated contrast is not precise enough to settle its direction. The registry record does not provide a more detailed assessment of the uncertainty or any adjusted primary analysis.

The trial was open-label, with masking listed as none. The registry record does not describe the method used to confirm eradication or whether outcome assessors were independent of treatment assignment. As a result, the registry entry alone does not permit assessment of possible influences of treatment awareness on outcome ascertainment.

Participant characteristics, detailed eligibility criteria, and participant flow are not fully reported in the registry record. The record does not state whether any randomized participants lacked an evaluable primary outcome, how missing data were handled, or which analysis population generated the posted results. These details are important when assessing the possibility of attrition or analysis-related bias.

Two secondary outcomes are listed, but their numerical results are not reported in the registry record. The analysis plan, multiplicity procedures, protocol-specific event definitions, and the original sample-size justification are also not reported. The safety information is limited to counts and does not describe event type, timing, severity beyond the serious-event distinction, or treatment relationship.

The trial’s urban New York City setting is documented, but detailed information needed to judge how well the participants represent other populations is not reported in the registry record. These limitations do not negate the posted comparison; they define the boundaries of what can be inferred from the registry entry alone.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: High Dose Dual Therapy vs Clarithromycin Triple Therapy for Treatment Naive H Pylori Infection in an Urban Population — NCT05342532.
• Registry record last updated 2023-02-01; status last verified 2023-01-05.
• Results first posted 2023-02-01.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

The registry describes a completed phase 4, prospective, randomized, open-label, parallel-group trial sponsored by Icahn School of Medicine at Mount Sinai. It enrolled 112 participants with treatment-naive H. pylori infection in a diverse urban New York City population.

The primary endpoint was the number of participants with eradication at the end of the study at 6 weeks. Eradication was recorded for 37 of 58 participants in High Dose Dual Therapy and 42 of 54 in Standard Triple Therapy. The posted risk difference was -0.140, with a 95% confidence interval from -0.306 to 0.026 and an unadjusted p-value of 0.105.

The registry also lists secondary adherence and adverse-event outcomes. Numerical results for the secondary outcomes, analysis-population definitions, missing-data methods, and the trial’s original sample-size assumptions are not reported in the registry record. The available results describe the observed comparison but leave uncertainty about its precision and about several aspects of the analysis.