The Effects of Increased Inoculum on Oral Rotavirus Vaccine Take and Immunogenicity: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Effects of Increased Inoculum on Oral Rotavirus Vaccine Take and Immunogenicity (NCT02992197), a randomized phase 4 study. The primary outcome is Number (or Percentage) of Infants in Each Study Arm Who Test Positive for Fecal Rotavirus Vaccine-strain Virus Shedding Post-vaccination.

2. Clinical Question

The trial focused on vaccine take and immunogenicity. For the posted primary endpoint, “take” was represented by a change in fecal shedding status: an infant who tested negative at baseline and positive at any later assessment counted as having the endpoint. The registry also describes serum rotavirus-specific IgA responses as an assessment of immunogenicity, but secondary outcome results are not reported in the registry record.

The comparison is between randomized dose regimens, rather than between vaccination and no vaccination. The registry identifies the study as a phase 4, randomized, parallel-group trial. Its title calls it double-blind, and its masking field records quadruple masking. Further details about which people were masked are not reported in the registry record.

3. Trial Design

The registry describes a completed phase 4 randomized controlled trial conducted in Dhaka, Bangladesh. It records an enrollment of 220 and dates the study from 2017-06-12 to a primary completion date of 2018-06-07. The design is parallel group, with infants assigned to receive either a standard or a double dose of Rotarix. The brief description states that assignment was 1:1. The registry describes the study as double-blind in its title and records quadruple masking in the masking field; additional operational details of masking are not reported in the registry record.

Both regimens involved oral vaccination at 6 and 10 weeks of life. The standard-dose group received 1.5 mL of Rotarix and 1.5 mL of placebo at each scheduled visit. The double-dose group received 3 mL of Rotarix at each visit, described as two standard doses administered simultaneously. Thus, the intended comparison was between dose levels within the same vaccine schedule.

The primary outcome was assessed through week 12 of life. Stool was collected before vaccination at weeks 6 and 10, then at 4, 7, and 14 days following each dose. Each specimen was tested for vaccine-strain virus by polymerase chain reaction. The primary endpoint definition counted an infant if shedding status changed from negative at baseline at 6 weeks to positive at any subsequent time point.

The posted primary outcome counts are 63 of 97.0 in the standard-dose arm and 55 of 92.0 in the double-dose arm. These endpoint denominators are distinct from the enrollment figure. Reasons that participants may not appear in those endpoint counts, and the analysis populations used, are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

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: The a priori primary analysis was designed to evaluate study outcomes among those who completed the study per-protocol. Due to anticipated levels of attrition, the per-protocol population differs from the total numbers of initial enrollees. Data presented are for the per protocol population.

6. Primary Endpoint

The registry lists the primary outcome as Number (or Percentage) of Infants in Each Study Arm Who Test Positive for Fecal Rotavirus Vaccine-strain Virus Shedding Post-vaccination, measured over Measured through week 12 of life.

The primary endpoint is the number or percentage of infants in each arm who tested positive for fecal rotavirus vaccine-strain virus shedding after vaccination. It is a binary participant-level outcome: each infant either met the stated definition or did not. The definition requires a negative shedding result at baseline at 6 weeks and a positive result at any later assessment. Testing was planned at multiple stool-collection times after the scheduled doses, through week 12 of life, using polymerase chain reaction.

Shedding is used in this trial as an indicator of vaccine take. The endpoint therefore captures detectable vaccine-strain virus in stool after vaccination, not a clinical disease outcome. It is also not the same as a measured serum antibody response. Although the registry describes serum rotavirus-specific IgA responses as part of the immunogenicity assessment, secondary outcome results are not reported in the registry record.

Repeated stool collection can detect a positive result at more than one follow-up time, but the primary outcome counts participants meeting the definition, rather than the total number of positive stool specimens. The endpoint description calls the measure an aggregate measure demonstrating change from baseline. It does not give separate posted results for each collection time or dose, so the record does not show when a participant first became positive or how long shedding continued.

7. Results Posted in the Registry

• Rotarix, Double Dose: 59.8% (55/92) versus 64.9% (63/97) on control; risk difference -5.2 percentage points (95% CI -19.0 to 8.6), risk ratio 0.92 (0.74–1.15); unadjusted two-proportion z-test p = 0.464.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is binary at the participant level: an infant either met the positive-shedding definition or did not. A comparison of two such groups can be expressed in several ways. The posted comparison includes a risk difference, a risk ratio, and an odds ratio. These are related but not interchangeable summaries, and each describes the contrast on a different scale.

What does the risk difference describe?

The risk difference is the absolute contrast between the proportions of participants with the endpoint in the two arms. In this registry comparison, the contrast is defined as double dose versus standard dose. A value below zero therefore points toward a lower observed endpoint proportion in the double-dose arm; a value above zero points toward a higher proportion in that arm. A value of zero corresponds to equal proportions. The posted risk-difference interval includes zero, so the data are compatible with no absolute difference as well as with differences in either direction.

How do ratio measures differ?

A risk ratio compares the endpoint probabilities as a ratio. A value of one corresponds to equal probabilities, while values on either side indicate a relative increase or decrease. An odds ratio compares odds rather than probabilities; odds are the ratio of the probability of an event to the probability of no event. When outcomes are not rare, an odds ratio can differ noticeably from a risk ratio and should not be interpreted as though it were a risk ratio. The registry posts both measures with intervals, but the absolute risk difference is often the most direct way to describe the size of an arm-to-arm contrast in percentage-point terms. No percentage-point conversion is needed to understand the direction of this posted estimate.

What does a confidence interval contribute?

A confidence interval describes the precision of an estimate under the statistical procedure used to construct it. It gives a range of values that are reasonably compatible with the data and that procedure; it is not a guarantee that the true value lies inside the observed limits. In this trial, the interval for the risk difference reaches across zero. That means the observed data do not clearly distinguish an effect in one direction from no difference or an effect in the opposite direction. The interval should be considered together with the estimate and the observed arm counts, rather than treated as a yes-or-no verdict.

What does the p-value tell the reader?

The posted unadjusted p-value is 0.464. In general, a p-value describes the probability, under a specified null model and its assumptions, of obtaining a result at least as incompatible with that model as the observed result. It is not the probability that the null model is correct, and it is not a measure of effect size. “Unadjusted” indicates that the posted value is not adjusted for a multiplicity procedure. The registry does not report the test method, whether this was the sponsor’s prespecified analysis, or any additional adjustment strategy.

Why can extra variation matter?

General statistical explanation: a binomial model treats each participant’s endpoint as an event or non-event and relies on assumptions about the relationship between the probability of an event and the variability of observed counts. In some data settings, outcomes vary more than a simple binomial model allows. This is called over-dispersion. If it is present but ignored, standard errors can be too small and confidence intervals can be too narrow, making results seem more precise than they are. The registry does not report an over-dispersion assessment or a model accounting for it; the binary endpoint description alone does not establish whether extra variation was relevant.

What is not specified about the analysis?

The registry lists zero analyses. It does not report the statistical test or model used for the primary comparison, covariate adjustment, the handling of repeated measurements, or the method used to construct confidence intervals. The endpoint definition combines positive results across follow-up times into a participant-level outcome, but detailed analysis code or specifications are not reported in the registry record. The displayed recalculated comparison is an unadjusted comparison from posted summary statistics; it should not be treated as evidence of the sponsor’s original statistical method. Because the discrepancy indicator is false, there is no noted conflict between the posted summary and that recalculation.

10. Confidence Intervals and Precision

The risk-difference confidence interval is the main guide to the precision of the posted arm comparison. Its limits extend from negative to positive values, crossing zero. This shows that the estimated direction is uncertain: the data remain compatible with a lower endpoint proportion under the double-dose regimen, little or no difference, or a higher proportion. The interval is not narrow enough to identify a precise magnitude or direction for the underlying contrast.

That uncertainty is consistent with the endpoint counts of 63 of 97.0 in the standard-dose arm and 55 of 92.0 in the double-dose arm. Those counts are the observed data, not exact estimates of what would occur in every similar group. Sampling variation means that another study could produce different proportions even if the underlying probabilities were unchanged. Confidence intervals are designed to convey some of that uncertainty under the method’s assumptions.

Precision is not the same as validity. An interval can quantify sampling uncertainty while leaving other uncertainties unresolved, such as missing outcome data, analysis-population choices, or limitations in the endpoint definition. The registry record does not report enough detail to assess those issues fully, nor does it report the method used for the primary interval. The interval should therefore be interpreted as the posted uncertainty summary, not as a complete account of all potential sources of uncertainty.

The p-value of 0.464 should not replace the interval. A p-value summarizes compatibility with a null model, while the interval shows a range of effect values compatible with the data under the interval procedure. Neither measure alone establishes equivalence or determines clinical importance. The registry does not report a threshold for a clinically important difference, so the clinical relevance of particular values inside the interval is not specified.

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 describe participants per arm, not total events. They are illustrations based on the observed effect, rather than the original trial’s design calculations. The assumptions listed for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a hypothetical study with an 80% chance of detecting the selected effect under the stated assumptions, if that effect is the true one. The 90% power column gives the corresponding per-arm planning figure for a 90% chance under those same assumptions. These are planning concepts, not guarantees for a future study; actual performance depends on whether the assumptions and effect size are appropriate.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The associated participants-per-arm figures are 1,380 and 1,847 for planning at 100% of the observed effect; 2,437 and 3,261 for planning at 75% of the observed effect; and 5,443 and 7,286 for planning at 50% of the observed effect, for 80% and 90% power respectively. Smaller effects need more participants to detect under the same assumptions, which is why the lower fractions correspond to larger planning figures. These calculations are not observed power.

The estimates are sensitive to the observed effect used as their starting point. Because the primary comparison is imprecise, planning directly from that estimate may produce unstable or impractical figures. The illustrations do not establish the number required for a definitive study, and they do not account for features not included in the listed assumptions. Any interpretation should keep their hypothetical planning purpose separate from the actual enrollment and endpoint counts in this trial.

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 = 0.649; treatment proportion p₁ = 0.598; average p̄ = 0.624.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6851 = 1.3429.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6842 = 0.5758.
4. n = (1.3429 + 0.5758)² / (-0.0517)² = 1,379.5, rounded up to 1,380 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 <- 0.649484536082474                          # control proportion
p1 <- 0.597826086956522                          # 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(2992197)
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 = 1,380 (80% power), 1,847 (90% power)
 75% of observed effect: n per arm = 2,437 (80% power), 3,261 (90% power)
 50% of observed effect: n per arm = 5,443 (80% power), 7,286 (90% power)
power.prop.test: 1379.5 
Simulated power at n = 1,380 per arm: 0.800 (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 describes several assessments, including fecal vaccine shedding and serum rotavirus-specific IgA responses. It identifies the shedding outcome as primary, but secondary outcome results are not reported in the registry record. The registry lists zero analyses. It therefore does not show a full set of outcome-specific estimates or indicate how many statistical tests were conducted beyond the posted primary comparison.

Multiplicity arises when many outcomes, time points, or comparisons are examined. General statistical explanation: the more hypotheses tested, the greater the chance that at least one result may appear unusual simply through random variation. Methods to address this can be prespecified, but the choice depends on the trial’s aims and analysis plan. A multiplicity strategy is not reported in the registry record, so the unadjusted p-value should not be described as multiplicity-adjusted or treated as a comprehensive test across all outcomes.

The primary endpoint combines results over several specimen collection times: a participant counts if the baseline result was negative and any subsequent result was positive. The registry does not report separate primary comparisons by specimen time or dose. It also does not specify how a missing specimen or an indeterminate test result was handled, whether participants with incomplete follow-up were included, or whether sensitivity analyses were performed. Those details are not reported in the registry record.

The endpoint denominators are 97.0 for the standard-dose arm and 92.0 for the double-dose arm, while the registry records enrollment of 220. The record does not explain the difference between enrollment and the outcome denominators, so reasons for absent endpoint data should not be inferred. Analysis-population definitions, including whether the posted comparison is intention-to-treat or based on another population, are not reported in the registry record.

The registry does not describe covariate adjustment, subgroup analyses, interim analyses, or a statistical analysis plan. These omissions do not establish that such procedures did or did not occur; they mean the details are not reported in the registry record. Without them, the posted comparison can be interpreted as a summary of the recorded outcome, but not as a complete reconstruction of all planned or conducted analyses.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: diarrhea (1.8%), sepsis (0.9%), subacute intestinal obstruction (0.9%), diaphragmatic hernia (0.9%).

The registry reports serious adverse event figures separately for the two dose groups. In the standard-dose group, 2 serious adverse events are recorded among 110 participants at risk; in the double-dose group, 4 are recorded among 110 participants at risk. The record lists zero deaths in each group. These figures are counts, not estimates of a causal effect of dose. They do not by themselves establish whether the groups differed in safety.

The registry also lists serious-event terms with percentages: Diarrhea, 1.8%; Sepsis, 0.9%; Subacute intestinal obstruction, 0.9%; and Diaphragmatic hernia, 0.9%. The listed terms are not mapped to a particular arm in the posted term list, so they should not be assigned to either group based on the information reported. The record does not provide enough detail in this listing to assess event timing, relatedness to vaccination, severity grading, or the event-level overlap between terms.

Other adverse events are recorded separately: 28 affected participants among 107 at risk in the standard-dose group and 31 among 106 at risk in the double-dose group. They should not be combined with the serious-event figures. Differences in denominators and event definitions matter when reading safety summaries, and the registry does not report additional analytic comparisons or an adjustment for the amount of follow-up.

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

The posted results describe fecal vaccine-strain shedding after two oral Rotarix dose schedules. The observed counts were 63 of 97.0 participants in the standard-dose arm and 55 of 92.0 in the double-dose arm. The posted comparison has a negative risk-difference estimate for double dose versus standard dose, with a confidence interval that crosses zero and an unadjusted p-value of 0.464. The result is therefore uncertain in both direction and magnitude.

These data do not demonstrate that the two regimens are equivalent. Equivalence requires a defined margin and an analysis designed to assess whether the plausible difference lies within that margin; such a margin and analysis are not reported in the registry record. Nor does the result show that one regimen is superior. The interval includes the possibility of differences in either direction, and the p-value alone cannot resolve that uncertainty.

The primary measure is a laboratory-defined shedding outcome, not a direct measure of clinical disease, illness severity, or protection. A positive stool test indicates detection of vaccine-strain virus under the endpoint definition, while a serum IgA response is a separate immunogenicity measure. Results for the IgA assessment and other secondary outcomes are not reported in the registry record. Consequently, the posted shedding comparison cannot answer whether the regimens differ on those outcomes.

The trial compared two dosing schedules in enrolled infants in Dhaka, Bangladesh. The record does not establish how well the results generalize to other populations, settings, schedules, or vaccine formulations. It also does not give enough information about missing endpoint data or the analysis population to evaluate their possible effects on the primary comparison. Interpretation should remain anchored to the measured endpoint and the limits of the posted statistical detail.

16. Why This Trial Matters Statistically

This trial illustrates an important distinction between a biological marker and a clinical outcome. The primary endpoint is fecal detection of vaccine-strain virus after vaccination. It can describe one aspect of vaccine take, but it is not itself a direct measure of illness or protection. Keeping the endpoint’s meaning clear prevents a laboratory result from being interpreted as though it answered every question about vaccine response.

It also shows why estimates and uncertainty need to be read together. The arm counts give the observed pattern, while the risk-difference interval indicates that the comparison is not precise enough to settle the direction or size of the underlying difference. A single point estimate can appear definitive when viewed alone; the interval gives essential context about the range of effects compatible with the data.

The trial’s dose comparison is relevant statistically because it assesses two active schedules rather than vaccination versus no vaccination. The groups share the same vaccine and timing, while the amount administered differs. The endpoint and the comparison therefore need to be interpreted within that specific design, not as a general estimate of vaccine effectiveness.

Finally, the registry illustrates how reporting completeness affects what can be concluded. The primary outcome counts and comparison are posted, but secondary results, analysis-population details, missing-data methods, and the original analysis plan are not reported in the registry record. Those gaps do not invalidate the posted numbers, but they limit assessment of how the outcome was analyzed and how broadly the findings can be interpreted. Clear separation of observed results, statistical uncertainty, and unreported design details is central to responsible trial interpretation.

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 result is limited to the participant-level shedding definition, which counts an infant if a baseline-negative result is followed by a positive result at any subsequent assessment. It does not distinguish the number of positive specimens, the timing of first detection, or the duration of shedding. Separate results by collection time are not reported in the registry record.

The posted endpoint denominators differ from the registry enrollment of 220, and reasons for that difference are not reported. Missing-data handling, participant flow, analysis-population definitions, and sensitivity analyses are also not reported in the registry record. Without these details, the effect of incomplete outcome data on the comparison cannot be assessed.

The record does not provide the primary statistical test or model, interval-construction method, adjustment strategy, or a detailed statistical analysis plan. It also does not report a clinically important difference for the endpoint. The confidence interval communicates uncertainty under its method, but the missing methodological details limit independent appraisal of that uncertainty.

Only the primary shedding results are posted; the registry describes IgA response assessment but does not report its results. The result therefore cannot be generalized to all measures of immunogenicity or to clinical outcomes. Safety listings are also limited: serious-event terms are not mapped to arms in the term summary, and further detail on event timing and relatedness is not reported. These are limitations of the available registry record, not evidence that unreported analyses or information do not exist elsewhere.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: The Effects of Increased Inoculum on Oral Rotavirus Vaccine Take and Immunogenicity — NCT02992197.
• Registry record last updated 2020-08-04; status last verified 2020-07.
• Results first posted 2020-07-17.
• 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 records NCT02992197 as a completed phase 4 randomized parallel-group trial sponsored by the University of Vermont. It reports enrollment of 220, a start date of 2017-06-12, and primary completion on 2018-06-07. The trial compared standard-dose and double-dose oral Rotarix at 6 and 10 weeks of life in infants in Dhaka, Bangladesh.

The primary endpoint was positive fecal vaccine-strain shedding through week 12 of life. The posted counts were 63 of 97.0 in the standard-dose arm and 55 of 92.0 in the double-dose arm. The posted risk-difference interval crosses zero, and the unadjusted p-value is 0.464. Secondary outcome results and several analysis details are not reported in the registry record.