A Study of Live Oral Cholera Vaccine, PXVX200 in Healthy Older Adults: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Live Oral Cholera Vaccine, PXVX200 in Healthy Older Adults (NCT02100631), a randomized phase 3 study. The primary outcome is Seroconversion Rate at Day 11.

2. Clinical Question

The registry describes the study as assessing immunogenicity and clinical acceptability of a single dose in older adults. Its brief summary frames the immune-response question in terms of antibody levels: whether older adults’ responses were similar to those in adults aged 18–45. That is a question about a measured immune marker, not a direct comparison of clinical cholera outcomes.

The primary comparison used historical data rather than a concurrently randomized younger-adult group. The older-adult study also included a placebo arm, but the posted primary endpoint results compare PXVX0200 in older adults with the historical adult group. The distinction matters: randomization can support comparisons between concurrent treatment groups, whereas historical comparisons may also reflect differences between studies or populations. The registry record does not report enough detail to evaluate those potential differences.

3. Trial Design

The registry identifies NCT02100631 as a completed Phase III, randomized, parallel-group study in healthy older adults. The official title describes it as double-blind and placebo-controlled; the registry’s masking field says quadruple masking. These are the record’s descriptions, and the registry does not explain the roles covered by the masking designation.

The study included older-adult groups assigned to PXVX0200 or placebo. PXVX0200 was described as a single-dose oral vaccine suspension, and the placebo as physiological saline. The overall enrollment is listed as 398. The primary immunogenicity result, however, is reported for the Immunogenicity Evaluable Population rather than as an analysis of the overall enrollment. The registry record does not provide the full IEP definition or explain how participants entered or left that population.

The primary endpoint comparison paired the older-adult PXVX0200 group with historical control data from adults aged 18–45. Those historical data came from subjects who received a single dose of PXVX0200 in study PXVX-VC-200-004 and were included as a bridging population for Day 11 seroconversion. Thus, the primary comparison is not the randomized vaccine-versus-placebo comparison in older adults. The registry does not post a placebo result for this primary endpoint in the listed primary results.

The registry record lists the primary endpoint as seroconversion rate at Day 11 and identifies geometric mean titer as a secondary outcome. It reports six outcome measures and four analyses, but those counts do not establish which analyses were prespecified or how they were selected. The statistical plan, original sample-size justification, non-inferiority margin, and interim-analysis plan 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.

Before assignment: This study included healthy volunteers (46 - 64 years) who were not previously immunized against cholera. A total of 398 subjects randomized, of which 299 received study treatment and 99 received placebo. A total of 36 subjects from the treatment group continued in the Immune Sub-study population. The historical control subjects are not included in the protocol enrollment number for PXVX-VC-200-005. They are solely a comparator population.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Immunogenicity Evaluable Population (IEP)

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 Seroconversion Rate at Day 11, measured over Day 11.

The primary endpoint is the percentage of participants with seroconversion at Day 11. Seroconversion was defined as a 4-fold or greater increase over baseline Day 1 SVA titer against the classical Inaba biotype of V. cholerae after one dose of Vaxchora vaccine. The endpoint was assessed in the Immunogenicity Evaluable Population.

This endpoint turns a laboratory antibody measurement into a binary outcome: each participant either met the specified rise criterion or did not. The reported rate is the proportion meeting that criterion. A binary endpoint is useful for expressing how often a defined immune response occurred in each group, while a geometric mean titer can describe the distribution of antibody levels in a different way. The registry lists GMT as a secondary outcome.

The endpoint was used to address an immunogenicity bridging question. The stated hypothesis was that the older-adult seroconversion rate would be non-inferior to the rate among adults aged 18–45 at Day 11. The endpoint therefore concerns the proportion meeting a prespecified antibody-rise definition, rather than the magnitude of every participant’s response or observed clinical protection from cholera. The registry record does not report the non-inferiority margin, so the threshold that would define an acceptable difference cannot be assessed from the record.

7. Results Posted in the Registry

• PXVX0200 in Older Adults: 90.4% (263/291) versus 93.5% (2512/2687) on control; risk difference -3.1 percentage points (95% CI -6.6 to 0.4), risk ratio 0.97 (0.93–1.00); unadjusted two-proportion z-test p = 0.046.

8. Statistical Interpretation

9. Statistical Methods Explained

For a binary endpoint, the event is whether each participant meets the defined criterion. In this study, the event was seroconversion: a 4-fold or greater rise from baseline Day 1 SVA titer against the classical Inaba biotype at Day 11. The rate is the number of participants meeting the criterion divided by the number evaluated in the relevant analysis population. The registry posts the rates and confidence intervals for the older-adult PXVX0200 group and the historical control group.

What does the risk difference express?

A risk difference subtracts one group’s event rate from another’s. It expresses the comparison on the absolute probability scale, which makes the result interpretable as a difference in percentage points when rates are reported as percentages. A negative risk difference in this comparison means the older-adult group’s estimated seroconversion rate was lower than the historical control’s. It does not, on its own, indicate whether that difference is statistically or clinically acceptable.

The sponsor reports a risk difference of -3.1 with a 95% confidence interval from -6.7 to 0.4. The registry gives the analysis type as non-inferiority. Non-inferiority asks whether the intervention’s outcome is not worse than the comparator by more than a prespecified acceptable amount. That amount is the non-inferiority margin. A confidence interval is interpreted against that margin, not only against zero. Because the margin is not reported in the registry record, the sponsor’s criterion cannot be independently checked from the posted result.

Why is a non-inferiority test different from a test of no difference?

A test of no difference evaluates whether the data are inconsistent with equal rates. A non-inferiority test instead evaluates whether the data rule out a loss larger than the accepted margin. These are different hypotheses and can lead to different conclusions. A p-value from an unadjusted recalculation of a difference does not answer the non-inferiority question unless the relevant margin and analysis are incorporated. The registry does not post the sponsor’s p-value for the non-inferiority analysis.

The recalculated p-value is based on the posted group summary statistics and is explicitly unadjusted. It should be read as a supplementary calculation, not as a replacement for the sponsor’s analysis. It also does not account for any analysis features that are not reported in the registry record. The discrepancy indicator is false, so the posted information does not flag a disagreement requiring the sponsor’s own analysis to take precedence over the recalculation. Even so, the sponsor’s stated analysis type and the recalculated test answer distinct statistical questions.

What do confidence intervals contribute?

A confidence interval describes uncertainty around an estimate under the assumptions of the method used. The rate intervals give plausible values for each group’s seroconversion rate, while the interval around the risk difference describes uncertainty in the between-group contrast. Wider intervals indicate less precision; narrower intervals indicate greater precision. These intervals do not guarantee that the true value lies within the reported limits, and they do not account automatically for sources of bias such as differences between a current study and a historical control.

The two group-specific intervals overlap, but overlap between separate confidence intervals is not itself a formal test of the difference. For a direct comparison, the interval for the risk difference is more relevant. Its inclusion of zero indicates that equal rates are among the values compatible with the estimate under that interval’s method. For non-inferiority, the key comparison would be between the lower confidence bound and the prespecified margin, which is unavailable in the record.

Why does the historical comparator matter statistically?

Random assignment helps balance participant characteristics between groups assigned within the same trial, on average. It does not make a historical group part of that randomization. Here, the older-adult groups were randomized to PXVX0200 or placebo, but the primary endpoint compares the vaccine group with adults aged 18–45 from an earlier study. The historical comparison may be affected by differences in population composition, study procedures, or other conditions across studies. The registry record does not report details sufficient to assess these possibilities.

The older-adult placebo group is relevant to the study design, but its presence does not turn the historical younger-adult comparison into a randomized one. Nor does the historical comparison provide a direct placebo-adjusted estimate of vaccine response in older adults. The listed primary result should therefore be interpreted according to the comparator actually used.

What does over-dispersion mean in general?

In general, over-dispersion occurs when observed variability is greater than a statistical model expects. When present, using a model that assumes less variability can make uncertainty look too small. A suitable analysis may need to account for the extra variability. The registry record does not report whether over-dispersion was relevant to this endpoint or whether any method to address it was used.

Likewise, the registry does not identify the method used to calculate the sponsor’s confidence interval or the details of the recalculation beyond its being unadjusted and based on posted summary statistics. Readers should not infer an unreported model, covariate adjustment, or sensitivity analysis from the displayed estimates.

10. Confidence Intervals and Precision

The older-adult PXVX0200 seroconversion estimate is 90.4%, with a 95% confidence interval of 86.4% to 93.5%. The historical control estimate is 93.5%, with a 95% confidence interval of 92.5% to 94.4%. The intervals communicate uncertainty in the group-specific rates; they are not ranges containing every individual participant’s result.

For the direct comparison, the sponsor reports a risk difference of -3.1 percentage points and a 95% confidence interval from -6.7 to 0.4. The interval spans values on either side of zero, so the estimated difference is not precise enough to exclude no difference under the reported interval. It also spans more than one possible direction of difference. The observed point estimate should therefore not be treated as an exact measure of the underlying contrast.

Precision and non-inferiority are related but distinct. A confidence interval may be too wide to support a conclusion even when its point estimate appears close to the comparator. To evaluate non-inferiority, the relevant limit of the interval must be judged against the prespecified margin. The margin is not reported in the registry record, so the interval’s precision relative to the sponsor’s acceptance criterion cannot be determined.

Moreover, statistical intervals quantify uncertainty under their analysis assumptions; they do not remove possible bias from comparing a current older-adult group with historical younger-adult data. The posted results support a description of the observed rates and their statistical uncertainty, but not a claim that all sources of uncertainty have been captured.

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 estimates are expressed as participants per arm, not as total events. They are illustrations based on the observed effect, not the original trial design. The registry record does not report the trial’s own sample-size justification or original planning assumptions.

The listed planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each planning scenario uses a stated fraction of the observed effect. For planning for 100% of the observed effect, the estimates are 1,204 participants per arm for 80% power and 1,611 participants per arm for 90% power. For planning for 75% of the observed effect, they are 2,046 participants per arm for 80% power and 2,738 participants per arm for 90% power. For planning for 50% of the observed effect, they are 4,389 participants per arm for 80% power and 5,876 participants per arm for 90% power.

The 80% power column gives the planned number per arm under which the calculation would have an 80% chance of detecting the specified effect if the assumptions and effect were true. The 90% column expresses the same idea at a higher target chance of detection, requiring more participants per arm under these scenarios. The curve should be read as a planning relationship between the effect targeted and the required sample size, not as an observed trial result.

Smaller effects require more participants because they are harder to distinguish from random variation. These calculations are not observed power. They do not show the probability that the completed trial’s result is correct or that a treatment effect exists.

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 = 0.935; treatment proportion p₁ = 0.904; average p̄ = 0.919.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3851 = 0.7549.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3845 = 0.3236.
4. n = (0.7549 + 0.3236)² / (-0.0311)² = 1,203.2, rounded up to 1,204 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 <- 0.934871604019352                          # control proportion
p1 <- 0.903780068728522                          # 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(2100631)
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 = 1,204 (80% power), 1,611 (90% power)
 75% of observed effect: n per arm = 2,046 (80% power), 2,738 (90% power)
 50% of observed effect: n per arm = 4,389 (80% power), 5,876 (90% power)
power.prop.test: 1203.2 
Simulated power at n = 1,204 per arm: 0.805 (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. Analyses Reported by the Sponsor

The registry reports the sponsor’s analysis as a non-inferiority risk difference of -3.1, with a 95% confidence interval from -6.7 to 0.4. It does not list a sponsor-reported p-value or the non-inferiority margin. The registry record therefore identifies the type of analysis and its estimate and interval, but does not provide all information needed to verify the decision criterion.

The unadjusted recalculation from the posted summary statistics gives p = 0.046 for a comparison of the rates. That recalculation is not the sponsor’s non-inferiority test: it addresses a test of difference rather than whether the interval excludes a loss beyond an acceptable margin. Its p-value should not be used as evidence that the sponsor’s non-inferiority criterion was met or missed.

The discrepancy indicator is false, so the registry does not flag a discrepancy between the sponsor’s result and the recalculation. The sponsor’s reported estimate and interval remain the primary record of the sponsor’s analysis, while the recalculation is a separate, unadjusted view of the posted summary statistics. Without the margin and full analysis details, neither the recalculation nor the reported interval alone allows an independent reproduction of the sponsor’s non-inferiority conclusion.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists six outcome measures and four analyses, and identifies geometric mean titer as a secondary outcome. It also states that one secondary outcome is posted. These counts describe the registry entries, but they do not establish how many statistical hypotheses were tested in the full study or which outcomes and analyses were prespecified.

The multiplicity strategy is not reported in the registry record. In general, when several hypotheses are tested, the chance of at least one false-positive result can increase unless the analysis plan addresses multiple testing. Whether that issue applies, and whether any correction or hierarchy was used, cannot be determined from the posted information. The unadjusted recalculated p-value should not be mistaken for a multiplicity-adjusted result.

The primary analysis population is the Immunogenicity Evaluable Population (IEP). The registry record does not provide its detailed eligibility rules, the handling of missing Day 11 measurements, exclusions from the population, or sensitivity analyses using another analysis population. These details matter because an evaluable-population analysis can differ from an analysis including all randomized participants, particularly if missingness or exclusions are related to response.

The registry also does not report the statistical analysis plan, interim analyses, or the original sample-size justification. It is therefore not possible to determine from the record whether the endpoint definitions, population, non-inferiority margin, or analysis choices were finalized before results were known. This absence is a limit on what can be assessed from the registry record, not evidence that a particular analysis choice was or was not made.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: atrial fibrillation (0.3%), spinal compression fracture (0.3%), myocardial infarction (0.3%).

For serious adverse events, the registry reports 3 among 296 participants at risk in the PXVX0200 older-adult group and 0 among 99 at risk in the placebo older-adult group. Deaths are reported as 0 in each group. These are descriptive counts and denominators in the registry’s safety record.

The registry lists atrial fibrillation, spinal compression fracture, and myocardial infarction among the top serious terms, each at 0.3%. The record does not specify in this listing which treatment group contributed each term, so the percentages should not be assigned to a particular arm. The registry also reports other adverse events in the group summaries, but those counts do not by themselves establish severity, causation, or a treatment-related pattern.

Serious adverse event counts are not a complete safety comparison. A zero count in one group does not show that risk is absent, and raw counts do not account for the uncertainty around uncommon events. These figures should be read as registry-reported observations rather than as proof of equivalence or causation. The safety population and follow-up details beyond the reported at-risk counts are not reported in the registry record.

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

The posted primary results show that 90.4% of the older-adult PXVX0200 group met the Day 11 seroconversion definition. The historical adult control rate is 93.5%. The sponsor’s risk-difference estimate is -3.1 percentage points, with a 95% confidence interval from -6.7 to 0.4. These estimates describe an antibody response criterion in the reported analysis populations.

They do not show the rate of clinical cholera, and they are not a direct estimate of protection against illness. The endpoint is an immune marker defined by a rise in SVA titer. The trial’s stated purpose was to assess immunogenicity and clinical acceptability, and the registry summary frames the protection question through antibody levels; the posted endpoint should not be interpreted as a clinical efficacy outcome.

The registry labels the sponsor analysis as non-inferiority, but the non-inferiority margin is not reported. Without that margin, readers cannot independently judge whether the uncertainty around the risk difference meets the trial’s criterion. A near-comparator point estimate does not itself demonstrate non-inferiority, and the unadjusted recalculated p-value addresses a different question.

The primary comparison also uses a historical control from adults aged 18–45, rather than a concurrently randomized younger group. Thus, the result is a cross-study comparison, and possible differences between the studies cannot be evaluated from the registry record. The older-adult placebo arm does not change the comparator used in the posted primary endpoint analysis.

The most defensible reading is that the registry reports a high observed Day 11 seroconversion rate in older adults, with uncertainty around both group rates and their contrast. The data do not establish clinical protection, do not eliminate the limitations of historical comparison, and do not allow independent verification of the sponsor’s non-inferiority decision without the margin and analysis details.

17. Why This Trial Matters Statistically

This trial raises a statistical issue common in immunogenicity research: whether an immune response in one population is sufficiently close to a response in another population to support a bridging interpretation. The endpoint is a defined antibody-rise criterion, and the comparison is framed as non-inferiority rather than simply as a test for any difference.

That distinction makes the margin essential. A non-inferiority claim depends on how much lower a response could be and still be considered acceptable. The estimate and confidence interval are reported, but the margin is not. The registry therefore illustrates why a point estimate and a p-value cannot replace the full design rule for a non-inferiority question.

The comparison also illustrates the methodological difference between concurrent randomization and historical controls. The older-adult study includes randomized vaccine and placebo groups, but the primary immunogenicity contrast uses historical data from younger adults. The result can inform a cross-population comparison, while remaining more exposed to study-to-study differences than a direct randomized comparison would be.

Finally, the confidence interval emphasizes that estimates carry uncertainty. The observed difference is not the only value compatible with the data, and the interval must be interpreted in the context of the endpoint, comparator, and decision margin. These considerations are important when translating a measured antibody response into a broader scientific interpretation.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary comparison uses historical control data from adults aged 18–45 rather than a concurrent randomized younger-adult group. Historical comparisons can be influenced by differences across studies, including differences in participant mix or study procedures. The registry record does not provide enough detail to evaluate whether such differences affected this comparison.

The posted primary results do not include the older-adult placebo group as the comparator. Although the trial is described as placebo-controlled and includes an older-adult placebo arm, the primary endpoint result presented is the older-adult PXVX0200 group versus historical control. The placebo arm therefore does not provide the direct comparator for the reported primary risk difference.

The non-inferiority margin is not reported in the registry record. The sponsor’s analysis is labeled non-inferiority, but without the margin readers cannot independently assess whether the confidence interval satisfies the planned criterion. The sponsor’s p-value and detailed statistical method are also not reported.

The endpoint is an antibody-based measure, not a clinical cholera outcome. The registry record does not establish how this measured seroconversion rate relates to clinical protection in the study population. The full definition of the Immunogenicity Evaluable Population, the handling of missing measurements, and sensitivity analyses are also not reported.

Finally, the registry does not report the original sample-size justification, full analysis plan, multiplicity approach, or interim-analysis plan. These omissions limit assessment of precision planning and analysis choices. They should be understood as limits of the registry record, not as evidence that the trial did or did not use any particular procedure.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study of Live Oral Cholera Vaccine, PXVX200 in Healthy Older Adults — NCT02100631.
• Registry record last updated 2023-06-28; status last verified 2023-06.
• Results first posted 2021-04-30.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT02100631 is a completed Phase III randomized study of PXVX0200 in healthy older adults. The registry describes parallel groups, quadruple masking, and a placebo arm; the official title describes the study as double-blind and placebo-controlled. Overall enrollment is 398.

The primary endpoint is Day 11 seroconversion, defined as a 4-fold or greater rise from baseline Day 1 SVA titer against the classical Inaba biotype. The reported primary comparison is older adults receiving PXVX0200 versus historical data from adults aged 18–45. The observed rates are 90.4% and 93.5%, respectively; the sponsor reports a risk difference of -3.1 with a 95% confidence interval from -6.7 to 0.4.

The registry classifies the sponsor’s analysis as non-inferiority, but the margin is not reported. The result is an immunogenicity comparison, not a clinical cholera outcome. The historical comparator and missing analysis details limit independent assessment of the non-inferiority conclusion.