Gastric Acid Suppression and Probiotic Colonization: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Gastric Acid Suppression and Probiotic Colonization (NCT03327051), a randomized phase 4 study. The primary outcome is Relative Abundance of VSL#3 Probiotic Bacterial Strains When Ingested in the Presence or Absence of the Proton Pump Inhibitor (PPI) Omeprazole at Week 4..

2. Clinical Question

3. Trial Design

This was a phase 4, randomized, quadruple-masked, parallel-group trial sponsored by Stanford University. Its title is “Gastric Acid Suppression and Probiotic Colonization,” and its official title is “The Effect of Gastric Acid Suppression on Probiotic Colonization.” The registry lists probiotics as the condition of interest. Enrollment was 39. The recorded start date was 2018-03-20, primary completion was 2018-12-30, and the trial status is completed.

The trial compared two treatment combinations. One arm received omeprazole and VSL #3; the other received placebo and VSL #3. Because both groups received the probiotic, the intended contrast concerns probiotic colonization in the presence or absence of gastric acid suppression, rather than probiotic exposure versus no probiotic exposure. The record identifies randomized allocation and quadruple masking, but it does not describe the allocation sequence, concealment procedures, or which trial roles were masked. Those details are not reported in the registry record.

The primary outcome was assessed at week 4 among participants who attended that visit. The registry describes a continuous endpoint and reports means and standard deviations by arm. It also lists secondary outcomes concerning symptoms related to VSL #3, bacterial phylum abundance, and metabolite peak intensity before and after probiotic administration. The registry record does not report the original sample-size rationale, the full visit schedule, or the detailed statistical plan. In particular, it does not specify the original design assumptions or describe whether interim analyses were planned.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Participants who attended the week 4 visit are included in the analysis.

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: Baseline characteristics were collected at visit 2 (week 0). Participants who attended visit 2 are included in the analysis.

6. Primary Endpoint

The registry lists the primary outcome as Relative Abundance of VSL#3 Probiotic Bacterial Strains When Ingested in the Presence or Absence of the Proton Pump Inhibitor (PPI) Omeprazole at Week 4., measured over Week 4.

The primary endpoint is the relative abundance of the combined bacterial strains in VSL #3, measured in stool samples at week 4. The registry defines relative abundance as the percentage of the listed probiotic strains within the bacteria sample following ingestion, with or without omeprazole. The listed strains are S. thermophiles, B. breve, B. longum, B. infantis, L. acidophilus, L. plantarum, L. paracasei, and L. delbrueckii subsp. bulgaricus.

This measure addresses the trial’s colonization question by quantifying how much of the sampled bacterial community is represented by the probiotic strains. It is a continuous outcome, so the registry reports the mean and standard deviation for each arm. A mean describes the average observed relative abundance in the analyzed group, while the standard deviation describes the spread of individual measurements around that mean. These summaries do not show the full distribution of participant-level values.

The endpoint is not a direct measure of symptoms or of a clinical benefit. Other listed outcomes concern symptoms and changes in bacterial or metabolite measures, but those are secondary outcomes. Interpretation of the primary endpoint is limited to the week 4 stool samples and the participants who attended that visit, as specified in the registry record.

7. Results Posted in the Registry

• Omeprazole and VSL #3: mean 1.00 versus 0.82 on control; difference 0.18 (95% CI -0.33 to 0.70), standardized effect d = 0.26; z-test p = 0.484.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous, and the registry summarizes it with a mean and standard deviation for each randomized arm. A mean is useful for describing the average level of relative abundance, while the standard deviation gives a sense of how dispersed the observed values were within each arm. These summaries are straightforward to interpret, but they do not reveal skewness, outliers, or other features of the individual-level distributions. Those features cannot be assessed from the registry summaries alone.

What does a mean difference represent?

A mean difference compares the arm-level averages on the outcome’s original scale. The posted recalculation is expressed as the mean for omeprazole and VSL #3 relative to the mean for placebo and VSL #3. A positive estimate indicates a higher observed average in the omeprazole arm in this coding; it does not, by itself, establish that the underlying groups differ. The estimate is unadjusted, meaning it is calculated from the posted arm summaries without a covariate adjustment.

Random allocation is intended to make the treatment groups comparable on average, but the registry record does not describe the randomization procedure or provide baseline characteristics. The direct estimate calculated from summary statistics is therefore a simple comparison, not evidence that all possible imbalances were addressed. Nor does it account for any analysis choices that may have been made using participant-level data, because those details are not reported in the registry record.

Why use a confidence interval?

A confidence interval describes the uncertainty around an estimated effect under the assumptions of the analysis. Its width reflects how precisely the data locate the estimate: narrower intervals indicate greater precision, while wider intervals leave a broader range of plausible values. The recalculated interval crosses the zero-difference value and extends on both sides of it. That means the summary-statistic recalculation is compatible with a range that includes either direction of difference. The registry does not state the confidence level associated with this interval, so no confidence percentage should be assigned to it.

A p-value addresses how unusual data at least as inconsistent with a specified null hypothesis would be under the assumptions of a test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The unadjusted p-value for the recalculated comparison is 0.484. Because the sponsor’s own analysis differs, the recalculated p-value should not displace the sponsor’s reported analysis. The registry’s two ANOVA p-values are attached to separate arm-specific analyses, not to the direct between-arm contrast, and the details of those analyses are not reported.

Why can variation matter?

Biological measurements can vary substantially between participants, and a standard deviation helps describe that observed variability. When variability is large relative to a difference in group means, an estimate is less precise unless there is substantial information in the data. The arm summaries report different standard deviations, but the record does not provide participant-level measurements or enough detail to assess distributional assumptions. In general, over-dispersion means that observed variability is greater than a model assumes. If a model ignores such extra variation, its uncertainty estimates can be too small and its inferential results too confident. This is a general statistical point; the registry does not report that over-dispersion was identified or modeled in this trial.

What does the analysis population imply?

The primary endpoint analysis includes participants who attended the week 4 visit. This is a visit-based analysis population, as described in the record. The registry does not say how missing week 4 measurements were handled, whether any imputation was used, or whether the analysis followed an intention-to-treat principle. Without those details, it is not possible to determine how absence from the visit or missing samples affected the estimates. The arm counts for the primary endpoint are reported separately from the adverse-event denominators, so those counts should not be treated as interchangeable.

The registry labels the trial randomized and parallel, but its record does not set out the full prespecified analysis plan. It does not report model diagnostics, covariate adjustments, handling of repeated or correlated measurements, or a prespecified strategy for multiple outcomes. The recalculation is therefore best understood as a simple, unadjusted reading of posted summary statistics, rather than a substitute for the sponsor’s full analysis.

10. Confidence Intervals and Precision

The recalculated mean difference is 0.183, with an interval from -0.330 to 0.697. The interval is broad relative to the point estimate and crosses zero, indicating that the posted summary-statistic comparison does not narrowly locate the between-arm difference. It includes values consistent with a lower average in the omeprazole arm and values consistent with a higher average. The registry record does not state the confidence level for this interval, so its coverage should not be described using a confidence percentage.

Precision is distinct from the direction of the point estimate. The observed means are higher in the omeprazole and VSL #3 arm, but the interval shows substantial uncertainty around the recalculated contrast. The p-value of 0.484 is also part of the unadjusted recalculation; it does not indicate the probability that there is no difference, nor does it express the importance of any difference.

The arm-level standard deviations are 0.840 and 0.523. They indicate observed spread around each arm’s mean, but the registry summaries cannot show the detailed shape of the data or whether a small number of observations strongly influenced the means. The endpoint analysis counts are 14 and 15, and the listed analysis population is participants who attended the week 4 visit. The precision of the estimate should be interpreted in that context.

Because the discrepancy flag is true, the sponsor’s own analysis takes precedence over the recalculated comparison. The registry does not report a direct sponsor estimate and interval for the between-arm contrast, or enough information to explain the difference between the analyses. Thus, the recalculated interval is useful as a transparent summary-statistic check, but it cannot resolve the sponsor’s analysis or replace details that are not reported in the registry record.

11. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not a total number of events. They illustrate how the required number per arm changes when planning around the observed effect or a smaller fraction of it. The registry lists estimates for planning around 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The corresponding figures for 80% power are 225, 400, and 900 participants per arm; the figures for 90% power are 302, 536, and 1,205 participants per arm.

In plain language, the 80% power column gives the illustrative participants per arm associated with an 80% chance of detecting the specified effect under the planning assumptions, if that effect is real and the assumptions hold. The 90% power column gives the analogous planning count for a 90% chance. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is the stated fraction of the observed effect.

As the target effect gets smaller, more participants are needed to distinguish it from sampling variation under the same assumptions. The planning estimates are based on the observed effect and do not describe the trial’s original design justification; that justification and the original design assumptions are not reported in the registry record. These figures are a planning illustration, not observed power.

The registry’s sample-size description distinguishes participant counts per arm from event totals in time-to-event calculations. This endpoint is continuous, and the reported planning figures are per arm. The estimates should be read as conditional illustrations rather than as a claim that the trial had those numbers or that the observed trial was designed around the posted effect.

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, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.183; pooled standard deviation σ = 0.694.
2. n = 2 × (1.96 + 0.842)² × 0.694² / 0.183² = 225.0, rounded up to 225 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
delta <- 0.1834                      # observed difference in means
sigma <- 0.694278709378515                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^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 (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3327051)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 225 (80% power), 302 (90% power)
 75% of observed effect: n per arm = 400 (80% power), 536 (90% power)
 50% of observed effect: n per arm = 900 (80% power), 1,205 (90% power)
power.t.test: 225.9 
Simulated power at n = 225 per arm: 0.800 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-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. Analyses Reported by the Sponsor

The registry flags a discrepancy between the sponsor’s own analysis and the unadjusted recalculation from the posted summary statistics. Under the stated interpretation of this flag, the sponsor’s own analysis takes precedence. The recalculated mean difference, interval, and p-value are simple, unadjusted calculations from the arm-level means, standard deviations, and analysis counts. They are useful for describing what those posted summaries imply, but they are not a replacement for the sponsor’s analysis.

The sponsor’s reported analyses are two arm-specific ANOVA results: p = 0.04 for omeprazole and VSL #3, and p > 0.99 for placebo and VSL #3. These results are not reported as a direct comparison between arms. A difference between separate within-arm p-values is not itself a test of the difference between arms, and the registry does not report the corresponding sponsor estimate for the primary between-arm contrast.

The record does not explain why the sponsor’s analyses and the recalculated result differ, nor does it provide the detailed model specifications or estimands needed to reproduce the sponsor’s analysis. The cautious reading is therefore to retain the sponsor’s analysis as authoritative where a discrepancy is indicated, while treating the recalculation as a descriptive check of the posted summaries. Neither should be interpreted beyond the outcome, population, and analysis details reported in the registry.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes, including symptoms related to VSL #3, bacterial phylum abundance, and metabolite peak intensity. It records 5 outcome measures and 4 posted secondary outcomes. Multiple outcomes can create multiplicity concerns because testing many hypotheses increases the chance of obtaining at least one apparently notable result by chance when no adjustment is made. This is a general statistical issue, not evidence that a particular adjustment was required or omitted in this trial.

The registry record does not report a multiplicity adjustment, a hierarchy of secondary hypotheses, or a strategy for interpreting multiple tests. It also does not describe whether the listed outcomes were all prespecified or how analyses were selected for posting. The original statistical plan is not reported in the registry record. Therefore, the role of multiplicity in the sponsor’s analyses cannot be established from the posted information.

The primary outcome population is stated as participants who attended the week 4 visit. The endpoint arm counts are 14 and 15. The record does not say whether all randomized participants were included in other analyses, whether any participants were excluded from the primary analysis beyond the visit-attendance criterion, or how missing measurements were handled. It does not report an imputation method, sensitivity analysis, or a complete accounting of missing primary outcome data. Those details are not reported in the registry record.

The two posted ANOVA results are described separately for the two arms. The record does not explain the question each ANOVA was intended to answer, identify the model terms, or connect those tests to a prespecified analysis plan. Because they are not presented as a direct between-arm test, they should not be treated as the primary randomized comparison. The distinction between the primary endpoint’s week 4 analysis and the other outcomes also matters: a result for one measure does not automatically establish a result for the others.

These gaps do not show that a particular method was or was not used. They limit how fully the posted findings can be audited and reproduced. A complete account of analysis populations, missing data, multiplicity, and modeling would be needed to interpret the full family of results with greater certainty.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry reports serious adverse events for the two treatment arms among those at risk. In the omeprazole and VSL #3 arm, 0 serious adverse events were reported among 19 participants at risk. In the placebo and VSL #3 arm, 0 serious adverse events were reported among 20 participants at risk. The record also reports 0 deaths in each arm.

These are counts recorded in the registry, not proof that serious events could not occur. Zero reported events in these groups leaves uncertainty about uncommon outcomes, and the figures should be read as observations from this trial rather than as a general safety estimate. The adverse-event denominators differ from the primary endpoint analysis counts, which are based on week 4 attendance; the registry does not explain the difference in those analysis populations.

The registry also reports other, non-serious adverse events: 7 in the omeprazole and VSL #3 arm and 9 in the placebo and VSL #3 arm. These counts are not rates, and no comparison or causal interpretation should be made from them alone. The serious adverse event figures do not establish that the treatment combinations are equally safe or that either combination has a particular safety profile beyond the reported observations.

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

The trial addresses a focused biological question: whether the relative abundance of VSL #3 bacterial strains in stool at week 4 differs when the probiotic is taken with omeprazole rather than with placebo. The posted means are 1.002 in the omeprazole and VSL #3 arm and 0.819 in the placebo and VSL #3 arm. The unadjusted recalculation gives a mean difference of 0.183, but its interval crosses zero and is broad. Taken together, the posted summaries offer an uncertain estimate of the between-arm contrast.

This endpoint concerns the measured representation of the listed probiotic strains in a stool sample. It does not, by itself, establish durable colonization, a change in symptoms, or a health benefit. The registry lists symptoms and other biological measures as secondary outcomes, but the primary endpoint should not be treated as a substitute for those outcomes. Nor can the result automatically be generalized beyond participants who attended the week 4 visit.

The trial was randomized and masked as recorded in the registry, but the available information does not include the detailed allocation process, participant characteristics, or complete statistical plan. The sponsor’s own analysis takes precedence over the recalculation because the record flags a discrepancy; however, the posted sponsor p-values are for separate arm-specific ANOVA analyses rather than a direct between-arm comparison. That reporting does not resolve the primary contrast on its own.

The registry therefore supports a limited statistical description: the arm-level averages, their observed spread, and an imprecise unadjusted recalculation of the mean difference. It does not support a definitive claim about a treatment effect, clinical value, or the persistence of probiotic strains. Missing-data handling, multiplicity procedures, and the rationale for the original sample size are not reported in the registry record, further limiting interpretation.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized clinical question and a posted result need to be matched carefully. The research contrast is omeprazole plus VSL #3 versus placebo plus VSL #3, with relative abundance at week 4 as the primary endpoint. Both groups receive the probiotic, so the comparison isolates the addition of acid suppression within the trial’s treatment combinations. That distinction helps prevent a mistaken reading of the study as probiotic versus no probiotic.

It also demonstrates the importance of identifying the estimand behind a statistical test. The registry’s two ANOVA p-values are arm-specific, while the clinical question concerns a between-arm difference. Separate within-arm tests do not directly answer that comparative question. A transparent estimate and interval from the arm summaries can help readers understand the direction and uncertainty of the contrast, but a flagged discrepancy means the sponsor’s own analysis must take precedence.

The endpoint is a continuous microbiological measure, not a patient-centered outcome. Its mean and standard deviation communicate average abundance and variation, while the interval communicates uncertainty around a recalculated contrast. The interval’s breadth highlights that point estimates alone can be misleading when precision is limited. The registry’s planning illustrations also show, in general terms, how targeting smaller effects requires more participants per arm under the stated assumptions.

Finally, the record makes clear that trial interpretation depends on more than a p-value. The analysis population is defined by week 4 attendance, but missing-data methods and multiplicity procedures are not reported. Those absences do not prove a flaw; they define what cannot be independently assessed from the registry record. Distinguishing observed data, recalculation, sponsor analysis, and unreported methodological details is central to sound statistical reading.

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 primary endpoint analysis is restricted to participants who attended the week 4 visit. The registry does not state how many participants lacked a week 4 measurement, why any visit was missed, or how missing outcome data were handled. Consequently, the relationship between attendance and the analyzed result cannot be assessed from the posted record. The primary endpoint arm counts are 14 and 15, while the adverse-event denominators are reported separately; the record does not explain the population differences.

The measurement is relative abundance in stool, which describes the representation of selected probiotic strains in the sampled bacterial community. It is not a direct measure of lasting colonization, symptoms, or clinical benefit. The record does not report further details of sample processing, measurement reliability, or how the endpoint behaved over time beyond the week 4 assessment. The listed secondary outcomes address additional biological and symptom measures, but their results are not included in the registry record for this analysis.

The sponsor’s reported ANOVA results are arm-specific, and the registry flags a discrepancy with the recalculation from summary statistics. The sponsor’s own analysis takes precedence, yet its model details and direct between-arm estimate are not reported in the registry record. This prevents a full reconciliation or independent reproduction of the sponsor analysis. The recalculation should therefore be understood as a simple unadjusted comparison rather than as a definitive replacement.

Further limitations specific to interpretation include the absence of reported participant characteristics, detailed allocation procedures, masking roles, original sample-size justification, and the complete statistical analysis plan. The record does not report multiplicity adjustment or missing-data sensitivity analyses. These are limits of the registry information; they should not be taken as evidence that a method was not used.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Gastric Acid Suppression and Probiotic Colonization — NCT03327051.
• Registry record last updated 2020-03-11; status last verified 2020-02.
• Results first posted 2020-01-07.
• 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

NCT03327051 is a completed phase 4 randomized, quadruple-masked, parallel-group trial sponsored by Stanford University. It compared omeprazole plus VSL #3 with placebo plus VSL #3. Enrollment was 39. The recorded start date was 2018-03-20, and primary completion was 2018-12-30.

The primary endpoint was mean relative abundance of the combined VSL #3 bacterial strains in stool samples at week 4, among participants who attended that visit. The posted arm means were 1.002 and 0.819. An unadjusted recalculation reports a mean difference of 0.183, an interval from -0.330 to 0.697, and p = 0.484. The record flags a discrepancy, so the sponsor’s own analysis takes precedence; its posted ANOVA p-values are arm-specific rather than a direct between-arm comparison.

The registry also lists secondary outcomes concerning symptoms, bacterial abundance, and metabolites. It reports no serious adverse events in either arm among the stated at-risk participants. Details of the original design assumptions, missing-data handling, multiplicity procedures, and full sponsor analysis are not reported in the registry record.