Evaluation of the Human Rotavirus Vaccine at Varying Schedules and Doses in Rural Ghana: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluation of the Human Rotavirus Vaccine at Varying Schedules and Doses in Rural Ghana (NCT01575197), a randomized phase 4 study. The primary outcome is Immunoglobulin A (IgA) Seroconversion: 6 & 10 Week vs. 6, 10, & 14 Week Vaccination Schedules.

2. Clinical Question

The registry describes a study of whether alternate HRV schedules could enhance immune response in a low-resource, high-burden African setting. The primary contrast focuses on adding a dose at 14 weeks to the schedule that already includes doses at 6 and 10 weeks. The outcome is an antibody response, not an observed measure of rotavirus illness or protection from illness.

The record also lists a schedule that begins HRV at 10 and 14 weeks. That schedule is not part of the primary comparison, though its IgA seroconversion result is listed as a secondary outcome. The registry’s stated primary question therefore concerns the three-dose schedule versus the earlier two-dose schedule, rather than all possible pairwise comparisons among the schedules.

3. Trial Design

The registry identifies this as a completed Phase 4, randomized, parallel-design study with no masking. PATH is listed as the sponsor. The recorded enrollment is 456. The study start is listed as 2012-09 and primary completion as 2013-02. The condition is rotavirus gastroenteritis.

Three HRV schedules are described: vaccination at 6 and 10 weeks; vaccination at 10 and 14 weeks; and vaccination at 6, 10, and 14 weeks. The primary endpoint compares the first and third schedules. The registry describes the study purpose as assessing whether alternate schedules could enhance vaccine immune response, including giving the two-dose schedule at a slightly older age and giving an additional dose.

Random allocation means that assignment to schedules was randomized, as recorded in the registry. Parallel design means participants were assigned to a schedule rather than the schedules being tested sequentially within each participant. The record says masking was none; it does not describe further procedures for allocation concealment or masking of outcome assessment. Those details are not reported in the registry record.

The primary analysis is described as per-protocol. Its stated criteria include meeting inclusion and exclusion criteria, pre-vaccination seronegativity, receiving HRV and oral polio vaccine according to the assigned group schedule, and attending visits within the specified windows. The registry’s description ends after an additional “and,” so any further criteria are not reported in the registry record. The registry does not report the original sample-size justification or the full statistical analysis plan.

Enrollment is a study-level registry figure and should not be mistaken for the number analyzed for every outcome. For the primary outcome, the arm-specific analysis counts are 142 in the 6 and 10 week group and 143 in the 6, 10, and 14 week group. Outcome-specific analysis counts can differ; for example, the secondary comparison involving the 10 and 14 week schedule lists 139 for that group.

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:

Analysis population for the primary outcome, as defined in the registry: Per-protocol analysis population--participants who (1) meet inclusion/exclusion criteria; (2) seronegative pre- vaccination; (3) concomitant administration of HRV and oral polio vaccine (OPV) according to Group schedule, (4) study visits in window periods (vaccination visits 4 weeks + 2 weeks), and (5) valid serology results.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: All enrolled subjects who received at least one rotavirus vaccine dose and are IgA seronegative (\< 20 U/mL) at 6 (Groups 1 and 3) or 10 (Group 2) weeks of age at baseline.

6. Primary Endpoint

The registry lists the primary outcome as Immunoglobulin A (IgA) Seroconversion: 6 & 10 Week vs. 6, 10, & 14 Week Vaccination Schedules, measured over 4-weeks post-vaccination (All Groups) and 8 weeks post-vaccination (6 & 10 week Group).

The primary endpoint is the percentage of participants with IgA seroconversion. The registry defines seroconversion as detection of anti-rotavirus IgA at a concentration of at least 20 U/mL after vaccination, among infants who were seronegative for anti-rotavirus IgA before vaccination. Measurement was by enzyme immunoassay. Thus, the endpoint records whether a participant crossed a specified antibody threshold, rather than the amount of antibody as a continuous measure.

The registry specifies assessment at 4-weeks post-vaccination for all groups and at 8 weeks post-vaccination for the 6 and 10 week group. Because the endpoint is a binary event, the reported percentage expresses the share of analyzed participants who met the seroconversion definition. The arm estimates are accompanied by 95% confidence intervals, which communicate uncertainty in the estimated percentages.

Seroconversion is used as an immunogenicity measure: it indicates a detectable antibody response under the study’s definition. It is not itself a direct measure of clinical disease, and the record does not establish from this endpoint alone how an antibody response relates to an individual infant’s protection from rotavirus gastroenteritis. The registry lists other immune measures and vaccine-type rotavirus shedding as secondary outcomes, but the primary question remains the comparison of seroconversion percentages between the two specified schedules.

7. Results Posted in the Registry

• Rotavirus Vaccine at Age 6,10,&14 Weeks: 43.4% (62/143) versus 28.9% (41/142) on control; risk difference 14.5 percentage points (95% CI 3.5 to 25.5), risk ratio 1.50 (1.09–2.07); unadjusted two-proportion z-test p = 0.011.

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.

IgA Seroconversion: 6 & 10 Week vs. 10 & 14 Week Vaccination Schedules

• 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:
  • Rotavirus Vaccine at Age 10 & 14 Weeks: 37.4% (52/139) versus 28.9% (41/142) on control; risk difference 8.5 percentage points (95% CI -2.4 to 19.5), risk ratio 1.30 (0.93–1.81); unadjusted two-proportion z-test p = 0.128.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Rotavirus Vaccine at Age 10 & 14 Weeks and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists six secondary outcomes spanning IgA seroconversion and geometric mean titers across schedules, the relationship between baseline IgG and post-vaccination seroconversion, vaccine-type rotavirus shedding in stool, and serious adverse event assessment. The only secondary numerical comparison described in detail in the available record is IgA seroconversion for the 6 and 10 week schedule versus the 10 and 14 week schedule. Numerical results for the other listed secondary outcomes are not reported in the registry record.

That secondary seroconversion comparison is directionally similar to the primary comparison in that its later schedule has a higher observed percentage than the 6 and 10 week schedule. Its registry-reported Fisher Exact p-value is 0.16. This broad pattern does not establish a consistent effect across all secondary endpoints: most of those outcomes have no numerical results in the record, and the endpoints measure different features of immune response, shedding, or safety.

Secondary outcomes can help describe whether a primary finding is accompanied by related patterns, but they are generally less decisive when many outcomes or comparisons are examined. Each additional test creates another opportunity for a result to appear noteworthy by chance. The registry does not report whether multiplicity adjustments were applied, whether the secondary analyses were prespecified in a hierarchy, or how the outcomes were prioritized. Therefore, the secondary p-value should be treated as exploratory context rather than as a stand-alone confirmation or refutation of the primary result.

The secondary outcomes also do not all answer the same question. Seroconversion is a threshold-based binary outcome, whereas geometric mean titers describe antibody levels, shedding concerns detection of vaccine-type rotavirus in stool, and serious adverse event assessment concerns safety. A pattern across these measures could be informative if the results and analysis details were available, but the registry record does not support a complete synthesis across them. The primary result should therefore be interpreted on its own terms, with the listed secondary outcomes viewed as additional questions rather than interchangeable replications.

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

• IgA Seroconversion: 6 & 10 Week vs. 10 & 14 Week Vaccination Schedules
• IgA Geometric Mean Titers (GMTs): 6 & 10 Week vs. 6, 10, & 14 Week Vaccination Schedules
• IgA GMTs: 6 & 10 Week vs. 10 & 14 Week Vaccination Schedule
• Baseline Immunoglobulin G (IgG) Levels: Impact on IgA Seroconversion Post-vaccination
• Vaccine-type Rotavirus Shedding in Stool
• SAE Assessment

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish the reported group estimates, the comparison test, and the planning illustrations. These are general explanations; the specific methods reported for this study are identified separately from what the registry does not describe.

What does a percentage estimate represent?

For a binary endpoint such as seroconversion, each analyzed participant either meets the stated event definition or does not. The reported group percentage estimates the proportion meeting that definition in that analysis population. The primary estimates are 28.9% for the 6 and 10 week schedule and 43.4% for the 6, 10, and 14 week schedule. The associated intervals describe uncertainty in estimating each group’s underlying percentage from the observed participants.

A group percentage does not by itself express the contrast between groups. A comparison can be expressed as an absolute difference in percentages, a ratio of risks, or an odds ratio, among other measures. The recalculated comparison information includes a risk difference, risk ratio, and odds ratio, but the registry’s own reported analysis is a Fisher Exact test. These measures answer related but distinct questions: absolute difference concerns the gap in event probabilities, a risk ratio compares probabilities multiplicatively, and an odds ratio compares event odds. They should not be treated as interchangeable.

What does Fisher’s exact test assess?

The registry reports Fisher Exact for the primary two-group analysis and for the listed secondary seroconversion comparison. In general, Fisher’s exact test evaluates whether the observed distribution of a binary outcome across groups is compatible with a null association, using the fixed margins of the corresponding count table. The resulting p-value is evidence against that null under the test’s framework; it is not an effect-size estimate and does not describe the precision of the group percentages. The registry does not report additional details about the test implementation or a complete statistical analysis plan.

The unadjusted recalculation uses posted summary counts and is a simple comparison, not a substitute for an analysis that might account for other design or analysis features. No adjustment variables are specified in the registry record for the posted primary result. Since the registry’s own analysis and the simple recalculation are not identical procedures, their p-values can differ without changing the observed direction of the arm percentages.

Why use a confidence interval?

A confidence interval gives a range of values compatible with the data and the method used to construct it, subject to the method’s assumptions. It is more informative than a point estimate alone because it shows the uncertainty associated with that estimate. The primary group intervals are 22.1% to 36.8% and 35.5% to 51.6%. They are intervals for the separate group percentages, not the registry’s reported interval for a treatment contrast. The registry reports no confidence interval for its Fisher Exact analysis.

In general, confidence intervals are not guarantees that a particular range contains the true value, nor do they assign a probability to a fixed parameter after the data have been observed. Their interpretation depends on the statistical procedure and sampling assumptions. For a comparison, a confidence interval for the difference would directly show which magnitudes of between-group contrast are compatible with the data. The registry’s own analysis does not report such an interval in the record.

Why might binary outcomes need other models?

For a binary endpoint, a basic analysis compares event proportions. Other analyses can model the probability of an event while adjusting for covariates or accounting for design features. A model choice should reflect the outcome and study design, and its assumptions should be checked. No adjusted model is specified in the registry record for the primary endpoint. The summary figures alone do not allow a reader to infer whether an adjusted analysis was planned or conducted.

Over-dispersion is a general issue when observed variability is greater than a model expects. In clustered or grouped data, outcomes within the same unit may be more alike than outcomes across units, making an independence-based model understate uncertainty. The registry record does not describe clustering or report an over-dispersion assessment for this study; no such feature should be assumed from the available information.

How should the reported and recalculated analyses be distinguished?

The registry reports Fisher Exact p = 0.014 for the primary comparison. A simple unadjusted recalculation from the posted summary statistics gives p = 0.011. The recalculated result is not a corrected version of the registry analysis; it is a separate calculation based on the posted counts. The record indicates no discrepancy flag, and the two values lead to the same broad direction of interpretation. They should nevertheless remain clearly labelled by source and method.

More generally, a statistical test does not answer whether the endpoint is clinically meaningful, whether the analysis population represents all enrolled participants, or whether multiple outcomes were considered. Those questions require information about outcome relevance, participant flow, and the analysis plan. Where these details are absent, interpretation should remain tied to what the registry actually reports.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimate. For the primary endpoint, the estimated seroconversion percentage is 28.9% in the 6 and 10 week group, with a 95% confidence interval from 22.1% to 36.8%. In the 6, 10, and 14 week group, the estimate is 43.4%, with a 95% confidence interval from 35.5% to 51.6%. These intervals indicate that the true group percentages are not known exactly from the observed data; the point estimates are only the central summaries.

The intervals are moderately broad, so a range of underlying response percentages remains compatible with each group’s data. The primary comparison is of interest because its group estimates differ, but separate group intervals are not a substitute for a confidence interval around the difference. The registry’s reported Fisher Exact result gives a p-value, not an interval for the comparison. The recalculated summary includes a risk-difference interval, but the registry’s own analysis does not report a confidence interval for that contrast.

In general, interval width depends on factors such as the amount of information in the data, event frequency, and the method used to estimate uncertainty. A narrower interval indicates greater precision under the chosen method; it does not guarantee that an estimate is unbiased or clinically important. A wider interval leaves more uncertainty about the plausible magnitude of the response. The registry does not report the interval-construction method for the arm percentages in the information.

Confidence intervals should also be read in relation to the population analyzed. The primary percentages come from the per-protocol population, not necessarily every participant enrolled or randomized. The recorded analysis counts are 142 and 143 for the primary comparison. The reported intervals therefore express uncertainty for those outcome estimates and do not remove uncertainty about generalizing beyond that analyzed population.

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 illustrations translate the observed primary effect into hypothetical sample-size requirements under stated assumptions. These figures are participants per arm, not total participants and not total events. The illustrations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They consider planning for 100%, 75%, or 50% of the observed effect.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect and the model assumptions were correct. The 90% power column describes the corresponding planning target for a 90% chance. These are design probabilities for hypothetical future studies, not probabilities that the observed result is true. The figures are not observed power.

For planning for 100% of the observed effect, the illustrations give 172 participants per arm for 80% power and 230 participants per arm for 90% power. For planning for 75% of the observed effect, they give 299 and 400 participants per arm, respectively. For planning for 50% of the observed effect, they give 656 and 877 participants per arm, respectively. The pattern reflects a general statistical principle: smaller effects are harder to distinguish from random variation, so more participants are needed to detect them at the same target power.

The curve associated with such planning calculations should be read as an illustration of how the required sample size changes with the assumed effect, not as a summary of trial performance. These figures were computed from the observed effect and are not the trial’s original design assumptions. The original sample-size justification and statistical planning details are not reported in the registry record. The figures also do not account for any design considerations beyond the listed assumptions.

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 = 0.289; treatment proportion p₁ = 0.434; average p̄ = 0.361.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6793 = 1.3314.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6715 = 0.5652.
4. n = (1.3314 + 0.5652)² / (0.1448)² = 171.5, rounded up to 172 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 <- 0.288732394366197                          # control proportion
p1 <- 0.433566433566434                          # 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(1575197)
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 = 172 (80% power), 230 (90% power)
 75% of observed effect: n per arm = 299 (80% power), 400 (90% power)
 50% of observed effect: n per arm = 656 (80% power), 877 (90% power)
power.prop.test: 171.5 
Simulated power at n = 172 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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison using Fisher Exact, with p = 0.014. A simple unadjusted recalculation from the posted summary counts gives p = 0.011. The recalculation is a separate analysis of the posted counts; it should not replace the registry’s reported result or be described as the sponsor’s analysis.

The two analyses point in the same direction because the observed seroconversion percentage is higher in the 6, 10, and 14 week group than in the 6 and 10 week group. Their p-values are close but not identical. Differences can arise because a recalculation and the reported analysis need not use the same test or implementation. The registry record does not give enough detail to attribute the numerical difference to a specific procedural choice.

The record indicates no discrepancy between the posted summary results and recalculated result. When such a discrepancy is flagged, the sponsor’s own analysis takes precedence; that condition does not apply to this comparison. In either case, p-values should be interpreted alongside the group estimates, confidence intervals, analysis population, and endpoint definition. A small p-value is not a measure of effect size or clinical importance, and neither result changes the fact that this endpoint measures antibody seroconversion rather than disease prevention.

15. Multiplicity, Missing Data and Analysis Populations

The study record lists a primary outcome and six secondary outcomes, with multiple comparisons across schedules and immune or safety measures. When several outcomes or pairwise comparisons are tested, the chance of at least one apparently unusual result can increase. This is the general multiplicity problem. Statistical approaches can control that risk, for example by adjusting significance thresholds or by defining a prespecified testing hierarchy, but the appropriate approach depends on the study aims and analysis plan.

Whether the investigators used any multiplicity adjustment, which outcomes were considered confirmatory, and whether comparisons followed a prespecified hierarchy are not reported in the registry record. The primary comparison should not be assumed to have been adjusted, or not adjusted, beyond the analysis information actually stated. The secondary p-value therefore deserves caution, particularly because the record does not describe a family-wise or other multiplicity strategy.

The primary endpoint uses a per-protocol population. Its described criteria include eligibility, seronegativity before vaccination, vaccination according to group schedule alongside oral polio vaccine, and visits within specified windows. The registry’s population description is incomplete, ending after an additional criterion begins; the remaining details are not reported in the registry record. The number and characteristics of participants excluded from the per-protocol analysis, reasons for exclusion, and handling of missing outcome data are also not reported in the registry record.

Per-protocol analysis can describe outcomes among participants meeting specified requirements, but its interpretation differs from an analysis based on all randomized participants. Excluding participants after randomization may affect comparability if exclusions relate to schedule, outcome, or other participant characteristics. The registry information does not allow assessment of whether this occurred. An intention-to-treat analysis, a missing-data method, or a sensitivity analysis is not described in the registry record and should not be presumed.

The original statistical analysis plan, interim analyses, and sample-size justification are not reported in the registry record. As a result, readers cannot establish from the registry alone whether all analyses were planned before results were known, how missing observations were handled, or whether the posted analysis population and tests follow the original protocol. These uncertainties do not invalidate the reported numbers, but they limit the ability to assess analysis choices and the robustness of the findings.

16. 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: acute respiratory infection (1.3%), gluteal abscess/ sepsis (1.3%), gastroenteritis (0.7%), abscess of the left jaw (0.7%), congenital hydrocephalus (0.7%).

The registry’s adverse-event information gives serious adverse events by group, with the number at risk and the number affected. The listed serious-event counts are 1 among 152 at risk in the 6 and 10 week group, 4 among 152 at risk in the 10 and 14 week group, and 3 among 151 at risk in the 6, 10, and 14 week group. These figures describe the registry’s recorded counts; they do not by themselves establish that vaccination caused an event or that group risks differ.

The registry also lists serious-event terms and percentages, including acute respiratory infection and gluteal abscess/sepsis at 1.3% each, and gastroenteritis, abscess of the left jaw, and congenital hydrocephalus at 0.7% each. The record does not provide enough detail to determine whether these terms are mutually exclusive, whether all events are represented, or how individual events were attributed. Serious adverse events should be distinguished from the separate “other” adverse-event counts, which are not serious-event counts.

Deaths are not reported in the registry record. Interpretation of safety is limited by the absence of fuller event descriptions, follow-up details, and analyses that compare event rates while accounting for uncertainty. These figures are descriptive and should not be used alone to infer comparative safety.

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

The primary result shows a higher observed IgA seroconversion percentage in the group assigned HRV at 6, 10, and 14 weeks than in the group assigned HRV at 6 and 10 weeks. The registry’s Fisher Exact test reports p = 0.014, and the simple unadjusted recalculation reports p = 0.011. The arm-specific confidence intervals show that each estimate remains uncertain. Taken together, the record supports describing an observed difference in this immunogenicity endpoint, while retaining uncertainty about its magnitude and generalizability.

The result does not establish that the three-dose schedule prevents more rotavirus gastroenteritis, reduces disease severity, or improves any other clinical outcome. The primary endpoint is antibody seroconversion according to a threshold definition. The registry does not provide a clinical efficacy result linking the observed antibody response to illness prevention. Nor does the result establish that every infant would have a stronger response under one schedule.

The comparison does not answer whether the three-dose schedule is preferable in all settings or for all infants. The study concerns a particular rural Ghana setting and uses a per-protocol analysis population. The registry record does not give all details needed to assess participant exclusions, missing data, or how closely the analyzed participants represent everyone enrolled. Generalization beyond the analyzed study population therefore requires caution.

The finding also should not be read as proof that the schedules are different in every relevant respect or that all secondary outcomes follow the primary pattern. The secondary seroconversion result involving the 10 and 14 week schedule has a different p-value, and numerical results for most listed secondary outcomes are not reported in the registry record. The primary result is one statistical contrast on one defined endpoint, not a complete account of immune response, clinical benefit, or safety.

Finally, statistical evidence and practical importance are distinct. A p-value describes compatibility with a null model, while the percentages and their intervals describe the observed response and its uncertainty. Determining the clinical meaning of an antibody response requires evidence beyond this endpoint. The registry record supports a careful account of the measured seroconversion result, not medical advice or a universal conclusion about vaccination schedules.

18. Why This Trial Matters Statistically

This trial illustrates how a randomized schedule comparison can address a focused immunogenicity question: whether adding a dose at 14 weeks, after doses at 6 and 10 weeks, is associated with a different observed antibody response. The result is expressed as a binary seroconversion percentage, making the endpoint easy to interpret as a share of participants meeting a defined threshold while also requiring attention to uncertainty and analysis population.

It also shows why effect estimates and tests should be read together. The group percentages communicate the observed responses, confidence intervals indicate uncertainty around those percentages, and Fisher Exact supplies a test of compatibility with a no-association hypothesis. A recalculation from summary counts gives a similar directional result but a different p-value. Keeping these quantities distinct prevents a test statistic from being mistaken for the size or importance of an effect.

The registry’s three schedules create more than one scientifically relevant comparison, and the record lists several secondary questions. That makes multiplicity and outcome hierarchy important to interpretation. Without a reported analysis plan or adjustment strategy, a secondary result should not be treated as independent confirmation simply because it is another endpoint from the same study.

The sample-size illustrations demonstrate how planning depends on the effect a future study aims to detect. Planning around a smaller effect requires more participants per arm under the stated assumptions. These calculations can inform design discussion, but they do not reveal the trial’s original rationale and are not a measure of power observed after the study.

Finally, the endpoint’s scope matters. The result concerns measured IgA seroconversion in a defined analysis population, not disease prevention. Separating biological response, clinical outcomes, and safety is central to sound interpretation of clinical-trial statistics.

19. 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 primary endpoint is an immunologic surrogate measure, defined by detection of anti-rotavirus IgA at at least 20 U/mL among participants seronegative before vaccination. The registry does not report a clinical disease outcome as the primary endpoint, so the result cannot directly quantify the effect of the schedules on rotavirus gastroenteritis.

The primary analysis is per-protocol, and the registry’s population description is incomplete. It does not report the full criteria after the final stated “and,” the number excluded from the analysis, reasons for exclusion, or the handling of missing endpoint data. Those omissions make it difficult to assess selection effects or reproduce the exact analysis population.

The record does not provide the original statistical analysis plan, sample-size justification, multiplicity strategy, interim analysis information, or full details of confidence-interval construction. It also does not describe whether analyses adjusted for participant characteristics or other design features. These missing details limit evaluation of prespecification and robustness.

Although three schedules are described, the primary result is a specific comparison of the 6 and 10 week schedule with the 6, 10, and 14 week schedule. The 10 and 14 week schedule appears in a secondary comparison, and numerical results for most other secondary outcomes are not reported in the registry record. The available information therefore does not support a complete comparison across all schedules and outcomes.

The safety data are presented descriptively, with limited event detail and no reported deaths. The record does not provide enough information to judge causality, completeness of follow-up, or comparative safety precisely. Finally, the study setting and analyzed population may limit generalizability; the registry information does not establish that the results apply unchanged to other populations or settings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Evaluation of the Human Rotavirus Vaccine at Varying Schedules and Doses in Rural Ghana — NCT01575197.
• Registry record last updated 2015-06-01; status last verified 2015-04.
• Results first posted 2015-06-01.
• 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.

23. Record Summary

NCT01575197 is a completed Phase 4 randomized, parallel-design study with no masking, sponsored by PATH. It evaluated HRV schedules in rural Ghana, with recorded enrollment of 456 and primary completion in 2013-02. The primary question compared IgA seroconversion for vaccination at 6 and 10 weeks versus vaccination at 6, 10, and 14 weeks.

Seroconversion was defined as detection of anti-rotavirus IgA at at least 20 U/mL after vaccination among participants seronegative before vaccination. The reported percentages were 28.9% and 43.4%, respectively. The registry reports Fisher Exact p = 0.014; a simple unadjusted recalculation gives p = 0.011. These results describe an antibody response in the per-protocol analysis population, not clinical disease prevention.

The record lists six secondary outcomes and descriptive adverse-event information, but numerical results for most secondary outcomes are not reported in the registry record. Details of the original sample-size rationale, full statistical plan, multiplicity handling, and missing-data approach are also not reported in the registry record.