Norovirus Bivalent-Vaccine Efficacy Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Norovirus Bivalent-Vaccine Efficacy Study (NCT01609257), a randomized phase 1, phase 2 study. The primary outcome is Percentage of Participants With Viral AGE Clinical Illness and Fecal Virus Excretion Detected by RT-PCR OR 4-Fold Rise In Anti-GII.4 Norovirus P Particle Antibody Titer.

2. Clinical Question

The endpoint combines symptoms with evidence of infection. A participant could meet its infection component through detection of virus in stool by RT-PCR or through a four-fold rise in anti-GII.4 norovirus P-particle antibody titer between the pre-challenge and post-challenge assessments. The symptom component included specified diarrhea or vomiting criteria, or combinations of vomiting and other symptoms. The registry describes symptom collection from challenge through discharge, with the challenge occurring at least 28 days after dose 2 and discharge at least 96 hours after challenge.

This is a question about outcomes under a controlled experimental challenge, not a direct estimate of illness after naturally occurring exposure. The registry record describes the study purpose as evaluating efficacy against acute gastroenteritis due to the challenge dose, alongside safety and immunogenicity. The results therefore need to be read in the context of the enrolled healthy adults, the challenge setting, and the composite endpoint definition.

3. Trial Design

The registry record describes a completed phase 1-2, randomized, multi-center, double-blind, placebo-controlled study with quadruple masking and a parallel-group model. Enrollment was 132. The study began on 2012-07-16, primary completion was 2014-03-01, and the status is completed. Takeda is listed as the sponsor.

Participants were assigned to the Norovirus Bivalent VLP Vaccine or saline placebo. The vaccine and placebo were each administered intramuscularly on Days 0 and 28. The study then used an experimental human Norovirus GII.4 challenge; the primary endpoint timeframe starts at the challenge dose, which was at least 28 days after the second dose, and extends through discharge, at least 96 hours after challenge. This design assesses outcomes after a planned challenge rather than following participants solely for naturally acquired infection.

The primary endpoint population was the modified intent-to-treat population, defined in the registry as participants who received at least one dose of study drug and were in the challenge stage. The posted primary endpoint denominators are 56 for the vaccine arm and 53 for placebo. Denominators can differ across outcomes: for example, the posted seroresponse results use 56 vaccine-arm and 51 placebo-arm participants. The reason for each denominator difference is not reported in the registry record.

The study lists 33 outcome measures and six analyses, while 25 secondary outcomes are posted. The registry record does not report the original sample-size justification, the planned statistical analysis details beyond the information shown for the reported analyses, or whether interim analyses were planned. Those details should not be inferred from the trial design or from the observed results.

4. Participant Flow and Accounting

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

Before assignment: Healthy Volunteers were enrolled equally in 1 of 2 treatment groups, Norovirus Bivalent VLP Vaccine or Placebo.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified intent-to-treat population (mITT) included all participants who received at least one dose of study drug, challenge stage.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Viral AGE Clinical Illness and Fecal Virus Excretion Detected by RT-PCR OR 4-Fold Rise In Anti-GII.4 Norovirus P Particle Antibody Titer, measured over Symptoms collected from Challenge dose (at least 28 days after dose 2) to discharge (at least 96 hours after challenge dose).

The primary endpoint is the percentage of participants who experienced viral acute gastroenteritis due to the GII.4 strain during the inpatient stay and met a clinical illness definition, together with evidence of infection. Infection evidence was defined as fecal virus excretion detected by RT-PCR or a four-fold rise in anti-GII.4 norovirus P-particle antibody titer from pre-challenge to post-challenge.

The clinical illness definition could be met by diarrhea, vomiting, or specified combinations of vomiting and other symptoms. Diarrhea was defined using stool frequency or stool weight criteria; vomiting was defined using episode frequency. The combined criteria also included nausea, fever, abdominal cramps or pains, abdominal gurgling or bloating, and myalgia. These rules turn a collection of symptoms and laboratory evidence into a binary endpoint: each participant either meets the composite definition or does not.

Using a composite can capture more than one clinically relevant manifestation of illness and infection. It also means the overall result does not isolate the contribution of any single symptom or infection measure. A participant could qualify through different combinations of clinical and laboratory findings. The registry record does not report separate primary-endpoint results for each component, so the posted primary comparison should be understood as applying to the composite as defined, rather than to any one symptom, RT-PCR result, or antibody response in isolation.

7. Results Posted in the Registry

• Norovirus Bivalent VLP Vaccine: 26.8% (15/56) versus 32.1% (17/53) on control; risk difference -5.3 percentage points (95% CI -22.4 to 11.8), risk ratio 0.84 (0.47–1.50); unadjusted two-proportion z-test p = 0.544.

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.

Severity of Viral AGE Due to GII.4 Strain Assessed by Modified Vesikari Scoring System During the Inpatient Phase

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Norovirus Bivalent VLP Vaccine: mean 4.40 versus 7.10 on control; difference -2.70 (95% CI -4.12 to -1.28), standardized effect d = -1.31; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Norovirus Bivalent VLP Vaccine than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With GII.4 Seroresponse Rate (4-fold Rise) From Pre-challenge Day 0 to Post-Challenge Day 30

• 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:
  • Norovirus Bivalent VLP Vaccine: 7.1% (4/56) versus 52.9% (27/51) on control; risk difference -45.8 percentage points (95% CI -61.1 to -30.5), risk ratio 0.13 (0.05–0.36); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Norovirus Bivalent VLP Vaccine than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span several domains: symptom severity, symptom duration, stool RT-PCR detection, antibody responses, and other immunogenicity measures. These outcomes complement the primary composite by describing aspects of illness, infection, and immune response that the primary endpoint combines or does not directly measure. They are not all interchangeable indicators of the same underlying question.

The numerical secondary results include a modified Vesikari severity score comparison and a GII.4 seroresponse comparison. Their definitions, scales, timeframes, and analysis populations differ from the primary endpoint. As a result, they should be interpreted as supporting context rather than pooled into a single secondary conclusion. The registry record lists further outcomes, but it does not report numerical results for every listed measure in the information available for these comparisons. Any overall pattern must be limited to what is actually posted and should not be generalized to unreported outcomes.

The secondary findings do not replace or resolve the uncertainty in the primary comparison. In particular, an antibody response is an immunogenicity measure, while the primary endpoint concerns a composite of clinical illness and evidence of infection after challenge. A result on one does not automatically establish the result on the other.

General statistical explanation: testing many secondary outcomes can increase the chance of chance findings when each is assessed separately. If an adjustment or prespecified hierarchy is not reported, isolated unadjusted results carry less evidential weight than a result interpreted within a clearly specified multiplicity strategy. The registry record does not report such a strategy, so the secondary results should be treated as exploratory context rather than as a collection of independent confirmations.

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

• Percentage of Participants With 4-Fold Rise In Serum P-Particle Antibody Titer by ELISA or Detection of Norovirus GII.4 by RT-PCR in the Stool
• Severity of Viral AGE Due to GII.4 Strain Assessed by Modified Vesikari Scoring System During the Inpatient Phase
• Severity of Viral AGE Due to GII.4 Strain Assessed by Post-Challenge Symptom Collection During the Inpatient Phase
• Duration of Viral AGE Due to GII.4 Strain During the Inpatient Phase
• Percentage of Participants With GII.4 Norovirus Positive RT-PCR in the Stool During the Inpatient and /or Outpatient Phase
• Percentage of Participants With GII.4 Seroresponse Rate (4-fold Rise) From Pre-challenge Day 0 to Post-Challenge Day 30
• Pan-Ig ELISA - Anti-Norovirus GI.1 VLP Geometric Mean Fold Rise (GMFR) From Baseline
• Percentage of Participants With Pan-Ig ELISA - Anti-Norovirus GI.1 VLP Seroresponse (4-fold Rise) From Baseline

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical methods are tools for expressing the observed comparison and its uncertainty. The registry identifies a Fisher Exact test for the primary comparison and a Wilcoxon (Mann-Whitney) test for the modified Vesikari score comparison. The recalculated estimates use the posted arm-level summary statistics and are unadjusted. The registry record does not report a full statistical analysis plan, so additional choices such as covariate adjustment, handling of all missing observations, or a hierarchy for secondary outcomes should not be assumed.

What does a risk difference describe?

For a binary outcome, the risk difference compares the proportion with the event in one arm with the proportion in the comparator arm. A negative value in the posted vaccine-versus-placebo comparison means the observed percentage was lower in the vaccine arm. The primary recalculation is -0.053. This is an absolute contrast on the risk scale, not a relative measure. It should be read with its confidence interval, which runs from -0.224 to 0.118. Since that interval includes zero, the data are compatible with no difference as well as with values on either side of zero under the calculation used.

Other measures can express the same binary comparison differently. A risk ratio compares the two risks as a ratio, while an odds ratio compares the odds. Such measures may look numerically different because they use different scales. They do not change the observed participant counts or eliminate uncertainty. The registry also reports percentages by arm; these are descriptive proportions in the analysis populations, not guarantees about outcomes for future participants.

Why is Fisher Exact reported?

Fisher Exact is a test for association between treatment group and a binary outcome. It evaluates the observed event counts under a null hypothesis of no association, using the data in the comparison. The registry reports p = 0.674 for the primary analysis. A p-value is not the probability that the null hypothesis is true, nor does it measure clinical importance. It is interpreted alongside the size of the estimated difference and the interval around that estimate.

The posted recalculation reports p = 0.544 for the primary comparison. This is not the registry’s Fisher Exact result. The registry record does not give enough detail to reconcile the two values, and they should remain clearly distinguished. The reported analysis and the recalculation are not interchangeable merely because both compare the same arms.

What does the mean difference for severity represent?

The modified Vesikari outcome is a score, summarized by a mean and standard deviation for each arm. The posted means are 4.4 for the vaccine arm and 7.1 for placebo; the recalculated mean difference is -2.7, with a 95% confidence interval from -4.122 to -1.278. A mean difference expresses the contrast on the score scale. The interval describes uncertainty around that estimate under the recalculation’s assumptions.

The sponsor-reported analysis for this score uses the Wilcoxon (Mann-Whitney) test, which is a rank-based method. It compares the distributions of observations by their ranks rather than relying directly on a normal-model comparison of the means. The posted registry p-value is 0.001, while the unadjusted mean-based recalculation reports p < 0.001. These tests do not answer precisely the same statistical question, so their results should be identified by method.

Why do multiple outcomes require caution?

When a study evaluates many endpoints, the chance of obtaining at least one apparently notable result by chance can increase if each is judged separately without adjustment. This is the general reason multiplicity matters. The registry lists many outcome measures, but does not report whether a formal multiplicity procedure was planned or used. Consequently, isolated secondary p-values should not be treated as if they had the same confirmatory status as a prespecified, multiplicity-controlled primary analysis.

General statistical explanation: a confidence interval is a range of values produced by a method that, over repeated studies under its assumptions, would cover the underlying parameter at the stated rate. It is not a probability statement about the fixed parameter after seeing these data. Wider intervals indicate less precision, while narrow intervals indicate more precision. Interpretation also depends on the quality of measurement, analysis population, and design.

General statistical explanation: over-dispersion occurs when observed variability is greater than a model expects. If a model assumes less variability than the data contain, standard errors can be too small and intervals too narrow. The registry record does not identify over-dispersion as a feature of these analyses, and no such adjustment should be inferred. The score comparison uses posted standard deviations and the binary comparison uses event proportions; those summaries do not establish that a particular model problem occurred.

11. Confidence Intervals and Precision

The primary recalculated risk difference is -0.053, and its 95% confidence interval extends from -0.224 to 0.118. The interval crosses zero, meaning that the posted data are compatible with a range of differences that includes no difference and also includes values favoring either arm. Its span signals substantial uncertainty around the point estimate. The point estimate alone should therefore not be read as a precise estimate of the effect.

Confidence intervals convey precision, not certainty. In general, an interval method describes the range of values reasonably compatible with the data under its assumptions. It does not mean that there is a 95% probability that the true value lies in this particular interval. Nor does it account for every possible source of uncertainty, such as measurement limitations or unreported analysis choices.

The primary arm denominators are 56 and 53, and the number of observed primary events is 15 and 17, respectively, in the posted recalculation. With a binary outcome, the amount of information depends on the observed event counts as well as the total participants. The resulting interval is therefore important context for the arm percentages of 26.8% and 32.1%.

Some secondary estimates have their own intervals and denominators. For the seroresponse outcome, the posted arm percentages are 7.1% and 52.9%, with arm-specific 95% confidence intervals of 2.0% to 17.3% and 38.5% to 67.1%. Its recalculated risk difference is -0.458, with a 95% confidence interval from -0.611 to -0.305. These intervals describe that secondary antibody-response outcome, not the primary composite endpoint. The score comparison has a recalculated mean-difference interval from -4.122 to -1.278.

Precision and statistical significance are related but not identical concepts. An interval can be informative about plausible effect sizes even when a test does not meet a conventional threshold, and a small p-value does not by itself show that an estimate is precise or important. Here, the primary interval’s inclusion of zero and its range of values are central to interpreting the primary comparison.

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 sample-size illustrations show participants per arm for the binary and continuous outcomes in this study; the general assumptions specify that time-to-event calculations, if present, are reported as total events. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row uses a stated fraction of the observed effect as the effect to detect. For example, the primary endpoint illustration for 100% of the observed effect gives 1,164 participants per arm for 80% power and 1,558 participants per arm for 90% power.

The 80% power column means that, under the stated assumptions and effect size, a study of that planned size would have an 80% chance of detecting an effect at the specified significance level if that effect were the true effect and the assumptions held. The 90% column describes the corresponding planning target with a higher chance of detection. These are planning illustrations computed from the observed effect, not the trial’s original design assumptions. The original sample-size justification is not reported in the registry record.

The rows that plan for 75% or 50% of the observed effect illustrate the consequence of targeting a smaller effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm to reach the same planned power under the calculation assumptions. The plotted curve expresses this general relationship across the illustrated effect sizes; it should be read as a planning aid rather than as a description of what happened in this trial.

These figures are not observed power. Observed power calculated from the final result would largely restate the observed estimate and its uncertainty, rather than provide an independent measure of evidence. The illustrations instead ask how large a future study would be under explicit assumptions. Their usefulness depends on whether the chosen effect and assumptions are appropriate for a future design.

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 = 0.321; treatment proportion p₁ = 0.268; average p̄ = 0.294.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6445 = 1.2632.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6434 = 0.5415.
4. n = (1.2632 + 0.5415)² / (-0.0529)² = 1,164.0, rounded up to 1,164 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 <- 0.320754716981132                          # control proportion
p1 <- 0.267857142857143                          # 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(1609257)
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 = 1,164 (80% power), 1,558 (90% power)
 75% of observed effect: n per arm = 2,097 (80% power), 2,807 (90% power)
 50% of observed effect: n per arm = 4,778 (80% power), 6,396 (90% power)
power.prop.test: 1164 
Simulated power at n = 1,164 per arm: 0.801 (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 a Fisher Exact test, with p = 0.674. The recalculated primary comparison is an unadjusted calculation from the posted summary statistics and reports p = 0.544, alongside a risk difference of -0.053 and a 95% confidence interval from -0.224 to 0.118. These should be described separately: the registry result is the reported analysis, while the recalculation is a supplementary summary-statistic comparison.

The values are not identical, and the registry record does not provide enough detail to reconcile them. The p-values can differ when analysis methods or calculation details differ; however, the record does not establish the specific reason for this difference. The sponsor’s reported analysis should therefore not be relabeled as the recalculation, and the recalculation should not be represented as the trial’s official analysis.

For the modified Vesikari score, the registry reports a Wilcoxon (Mann-Whitney) test with p = 0.001. The recalculation is based on the posted means and standard deviations and gives p < 0.001 for a mean difference of -2.7. The rank-based registry test and mean-based recalculation use different summaries and methods. For the seroresponse outcome, no sponsor-reported analysis is listed, while an unadjusted recalculation is available. The registry record does not report a sponsor analysis for that comparison.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 33 outcome measures, reports six analyses, and has 25 secondary outcomes posted. Testing or estimating a range of outcomes can be useful because it describes different features of the study, but it also raises questions about multiplicity. When many hypotheses are tested separately, some results may look notable by chance even if there is no corresponding underlying difference. This is a general statistical concern, not evidence that any particular result in this study is false.

The registry record does not report whether the study used a multiplicity adjustment, a prespecified hierarchy among outcomes, or another procedure to control interpretation across multiple comparisons. It also does not report the complete statistical analysis plan. The primary endpoint remains the central outcome named in the record, but the details of how secondary claims were prioritized are not reported in the registry record. Unadjusted secondary p-values should therefore be interpreted cautiously and should not be counted as independent confirmations.

The primary analysis population is described as modified intent-to-treat: participants who received at least one dose of study drug and entered the challenge stage. The posted primary endpoint denominators are 56 and 53. The seroresponse outcome uses denominators of 56 and 51. The reason the denominators vary is not reported in the registry record. It is therefore not possible to determine from these results alone whether the differences reflect missing measurements, eligibility for a particular analysis, or another reason.

The registry record also does not report the detailed missing-data handling rules for each endpoint. No assumption about how missing values were treated should be made. For the same reason, the posted percentages should be understood as the results for their stated analysis denominators, rather than as percentages recalculated for all enrolled participants.

These omissions affect how fully the analysis can be evaluated, especially for secondary outcomes and differing denominators. They do not invalidate the numerical results, but they limit the ability to assess whether every analysis followed a prespecified plan and how missing observations may have influenced particular estimates.

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 2% reporting threshold.

Most frequent non-serious adverse event terms

The posted serious adverse event counts are zero in the vaccine group and zero in the placebo group. The serious-event populations at risk are 67 for the vaccine group and 65 for placebo. The registry also reports 10 participants with other adverse events among 67 at risk in the vaccine group and seven among 65 at risk in the placebo group. These are descriptive counts in the safety data, and the categories should not be conflated: the other adverse-event counts are not serious adverse event counts.

The registry record does not report deaths in these safety fields. The list of top serious adverse event terms is empty. These entries describe what is recorded; they do not establish that no events of any kind occurred beyond the categories and reporting shown, nor do they establish a causal relationship between an event and study treatment.

Safety counts require attention to the population at risk and the duration and method of collection. The registry record describes symptom collection during the inpatient challenge phase for the primary endpoint, but the safety summary does not provide further detail about follow-up duration or event definitions. The counts therefore support a limited descriptive reading, not a comprehensive assessment of safety across other settings.

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

The primary data show that the posted percentage meeting the composite endpoint was 26.8% in the vaccine arm and 32.1% in the placebo arm. The recalculated risk difference is -0.053, with a 95% confidence interval from -0.224 to 0.118. The interval includes zero and permits values in either direction, so the estimate is not precise enough to establish a clear arm difference from these data alone. The registry’s reported Fisher Exact p-value is 0.674.

This result applies to the study’s defined composite endpoint in a controlled experimental GII.4 challenge among healthy adults. It combines clinical illness criteria with evidence of infection by RT-PCR or antibody rise. It does not separately estimate every component, and it does not directly describe disease after naturally occurring exposure. It also does not settle questions about other populations or other norovirus strains.

The secondary outcomes provide additional descriptions of severity and immune response, but they address distinct measurements and should not be used to override the primary result. The registry record does not report a multiplicity strategy, and some listed secondary outcomes do not have numerical results in the posted comparisons. These factors limit the strength of broader conclusions drawn from secondary findings.

Statistical interpretation is not individual medical advice. A group-level comparison does not predict an individual participant’s outcome, and the estimates do not determine whether an intervention is appropriate for any person. The results describe the observed study data and the uncertainty around selected comparisons, within the design and analysis populations recorded.

18. Why This Trial Matters Statistically

This trial illustrates how a clinical endpoint can combine symptoms and laboratory evidence into one binary outcome. That structure is statistically important: it makes the endpoint broader than any single symptom or test, while also making the overall estimate dependent on multiple routes to meeting the definition. The composite’s rules are therefore essential to interpreting its percentages and risk difference.

It also demonstrates why the point estimate, confidence interval, and p-value should be read together. The primary arm percentages differ descriptively, but the recalculated interval crosses zero and the registry reports a Fisher Exact p-value of 0.674. The point estimate alone would conceal the uncertainty; a p-value alone would conceal the range of effects compatible with the data. Together, they offer a more complete account of the primary comparison.

The record further shows the distinction between sponsor-reported analysis and an unadjusted recalculation. The posted primary p-values differ, and the registry record does not explain the difference. Clear labeling of methods and results prevents a supplementary calculation from being mistaken for the trial’s formal analysis.

Finally, the study has many outcomes spanning illness, infection, and immune response. Those outcomes can enrich the scientific description, but they also make multiplicity and outcome prioritization important. When the registry record does not report a multiplicity strategy or full analysis plan, statistical conclusions should remain closely tied to the clearly defined primary endpoint and to the methods actually reported.

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 study used an experimental Norovirus GII.4 challenge in healthy adults. This controlled setting provides a defined exposure context, but the results do not directly establish what would happen with naturally acquired norovirus infection or in populations not described in the registry record. The study’s title and summary identify healthy adults; further participant characteristics are not reported in the registry record.

The primary endpoint is a composite that combines specified illness criteria with evidence of infection. It can be met through RT-PCR detection or a four-fold antibody rise, alongside the clinical definition. Because the components can qualify participants through different routes, the composite result does not show the separate contribution of each symptom, laboratory measure, or antibody criterion. Separate primary component results are not reported in the registry record.

The primary comparison has 56 participants in the vaccine arm and 53 in placebo, with 15 and 17 events in the recalculation. The resulting confidence interval is broad and includes zero. This limits precision about the size and direction of the difference. Denominators also vary across posted outcomes; the reason for the seroresponse denominator difference is not reported in the registry record.

The registry record does not report the original sample-size justification, full statistical analysis plan, multiplicity procedure, interim analysis details, or detailed missing-data rules. These omissions limit evaluation of how the analyses were planned and how secondary outcomes and missing observations were handled. The sample-size illustrations are based on the observed effects and are not evidence about the assumptions used to design this trial.

Finally, the registry lists more outcomes than have numerical comparisons described in the posted results. Conclusions about unreported outcomes cannot be drawn from the listed outcome names alone. The evidence should be confined to the endpoints and comparisons for which results are recorded.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Norovirus Bivalent-Vaccine Efficacy Study — NCT01609257.
• Registry record last updated 2019-01-09; status last verified 2019-01.
• Results first posted 2016-08-15.
• 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

NCT01609257 is a completed phase 1-2 randomized, multi-center, double-blind, placebo-controlled study of intramuscular Norovirus Bivalent VLP Vaccine versus saline placebo in healthy adults, followed by experimental GII.4 challenge. The primary outcome was a composite percentage with clinical viral acute gastroenteritis and evidence of infection. Posted primary percentages were 26.8% for vaccine and 32.1% for placebo; the recalculated risk difference was -0.053, with a 95% confidence interval from -0.224 to 0.118. The registry reports Fisher Exact p = 0.674. The interval includes zero, and the comparison is imprecise. Secondary outcomes address severity and immune response, among other measures, but multiplicity procedures and several elements of the analysis plan are not reported in the registry record.