Immunogenicity & Safety of GSK's Avian Flu Vaccine 1557484A Given to Adults Aged ≥18 Years: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Immunogenicity & Safety of GSK's Avian Flu Vaccine 1557484A Given to Adults Aged ≥18 Years (NCT00719043), a randomized phase 2 study. The primary outcome is Number of Seroconverted Subjects for Haemagglutination Inhibition (HI) Antibodies Against the A/Turkey/Turkey/1/2005 (A/Turkey) Virus Strain..

2. Clinical Question

3. Trial Design

The registry record describes a randomized, double-masked, parallel-group Phase 2 trial of monovalent H5N1 vaccine in adults aged at least 18 years. Enrollment was 841. The study was listed as completed, with a start date of 2008-07-11 and primary completion date of 2010-04-22. GlaxoSmithKline was the sponsor, and influenza was the listed condition.

Several vaccine schedules and formulations were studied. The arm descriptions include A/Indonesia priming followed by A/turkey vaccine or placebo at Day 182, and a naïve schedule involving placebo at Day 0 and A/turkey vaccine doses later. For the primary outcome, however, the registry specifically identifies four A/Indonesia-primed groups: one received A/turkey formulation 3 at Day 182 and placebo later, while the other three received placebo at Day 182 and an A/turkey vaccine formulation later. The primary endpoint was assessed at Day 559, using Day 549 as its pre-vaccination reference.

The registry record says the protocol posting was updated following Amendments 1-3 of the Protocol, Dec 2009, and that the impacted sections were study design and outcome measures. The original allocation schedule, masking procedures in operational detail, and the trial’s original statistical design assumptions are not reported in the registry record. The randomized, double-masked, parallel description identifies broad design features but does not by itself explain how allocation was generated, who remained masked, or how the groups were managed.

The record lists 32 outcome measures and 21 posted secondary outcomes. It includes antibody outcomes at different assessment times, but reported analyses for the posted secondary results are not listed. The trial design and endpoint descriptions therefore provide useful context for the comparisons, while leaving some details of implementation and analysis unreported.

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.

Only the first 6 of 7 groups are shown.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The analysis was performed on the According-to-Protocol cohort for immunogenicity, i.e., all evaluable subjects with at least Day 182 and 192 or Day 549 and 559 haemagglutination inhibition (HI) titer results for the A/turkey/Turkey/1/05 virus.

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.

Only the first 6 of 8 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Number of Seroconverted Subjects for Haemagglutination Inhibition (HI) Antibodies Against the A/Turkey/Turkey/1/2005 (A/Turkey) Virus Strain., measured over At Day 559.

The primary endpoint counts subjects who seroconverted for HI antibodies against the A/Turkey/Turkey/1/2005 virus strain at Day 559. Seroconversion was defined using the subject’s pre-vaccination and post-vaccination titers. A subject qualified if the pre-vaccination titer was less than 1:10 and the post-vaccination reciprocal titer was at least 1:40, or if the pre-vaccination reciprocal titer was at least 1:10 and the post-vaccination titer had increased at least four-fold. For this endpoint, pre-vaccination refers to Day 549.

This is a binary immunogenicity outcome: each evaluable subject either met the stated seroconversion definition or did not. Counting subjects meeting a prespecified antibody response definition makes the result straightforward to describe across groups. It is not the same as comparing the full distribution of antibody titers, and it does not directly measure clinical illness or protection from influenza.

The analysis population was the According-to-Protocol cohort for immunogenicity. The record defines it as all evaluable subjects with at least Day 182 and Day 192 or Day 549 and Day 559 HI titer results for the A/turkey/Turkey/1/05 virus. Thus, the posted endpoint is tied to the availability of specified measurements and to the protocol-based evaluability definition, rather than simply to everyone enrolled. The registry record does not report the endpoint’s clinical validation or a threshold linking these antibody results to clinical outcomes.

7. Results Posted in the Registry

• A/Indonesia Primed-Placebo-A/Turkey Influenza (H5N1)-F1-Group: 93.1% (81/87) versus 85.5% (71/83) on control; risk difference 7.6 percentage points (95% CI -1.7 to 16.8), risk ratio 1.09 (0.98–1.21); unadjusted two-proportion z-test p = 0.109.
• A/Indonesia Primed-Placebo-A/Turkey Influenza (H5N1)-F4-Group: 91.2% (73/80) versus 85.5% (71/83) on control; risk difference 5.7 percentage points (95% CI -4.1 to 15.5), risk ratio 1.07 (0.95–1.19); unadjusted two-proportion z-test p = 0.256.
• A/Indonesia Primed-Placebo-A/Turkey Influenza (H5N1)-F2-Group: 90.3% (65/72) versus 85.5% (71/83) on control; risk difference 4.7 percentage points (95% CI -5.5 to 14.9), risk ratio 1.06 (0.94–1.19); unadjusted two-proportion z-test p = 0.370.

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.

Number of Seroprotected Subjects for Haemagglutination Inhibition (HI) Antibodies Against the A/Turkey/Turkey/1/2005 (A/Turkey) Virus Strain.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Pumarix Primed-A/Turkey H5N1-Formulation 2-Placebo Group: 95.3% (82/86) versus 92.1% (82/89) on control; risk difference 3.2 percentage points (95% CI -3.9 to 10.4), risk ratio 1.03 (0.96–1.12); unadjusted two-proportion z-test p = 0.381.
  • Naïve Placebo-A/Turkey H5N1-Formulation 3 Group: 61.2% (60/98) versus 92.1% (82/89) on control; risk difference -30.9 percentage points (95% CI -42.1 to -19.8), risk ratio 0.66 (0.56–0.79); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pumarix Primed-A/Turkey H5N1-Formulation 2-Placebo Group and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Naïve Placebo-A/Turkey H5N1-Formulation 3 Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Seroconverted Subjects for Haemagglutination Inhibition (HI) Antibodies Against the A/Turkey/Turkey/1/2005 (A/Turkey) Virus Strain.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Pumarix Primed-Placebo-A/Turkey H5N1-Formulation 1 Group: 90.9% (80/88) versus 84.1% (69/82) on control; risk difference 6.8 percentage points (95% CI -3.2 to 16.7), risk ratio 1.08 (0.96–1.21); unadjusted two-proportion z-test p = 0.181.
  • Pumarix Primed-Placebo-A/Turkey H5N1-Formulation 4 Group: 87.5% (70/80) versus 84.1% (69/82) on control; risk difference 3.4 percentage points (95% CI -7.4 to 14.1), risk ratio 1.04 (0.92–1.18); unadjusted two-proportion z-test p = 0.541.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pumarix Primed-Placebo-A/Turkey H5N1-Formulation 1 Group and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Pumarix Primed-Placebo-A/Turkey H5N1-Formulation 4 Group and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover related but non-identical aspects of the antibody response, including seroprotection and seroconversion at assessment times other than the primary Day 559 endpoint. The comparisons also involve different vaccine schedules and analysis groups. They should therefore be read as a collection of complementary observations, rather than as repeated measurements of precisely the same primary question.

The overall pattern is mixed. Some comparisons have estimated differences near zero with intervals that include zero, while the Day 224 comparison involving the naïve placebo/A-turkey formulation 3 group is more clearly separated from its listed reference on the posted interval. That contrast is not the primary Day 559 endpoint, and its population and timing differ. It can add descriptive context about the measured antibody response, but it does not resolve the uncertainty in the primary comparisons.

The relationship to the primary result is therefore one of context, not confirmation or contradiction. The primary endpoint asks about seroconversion at Day 559 in specified A/Indonesia-primed groups. Secondary seroprotection and other-timepoint seroconversion outcomes ask related questions using different definitions or times. A difference in one secondary comparison does not imply the same contrast at Day 559, and a secondary interval that includes zero does not negate the observed primary estimates.

Unadjusted secondary results carry less weight because many outcomes and comparisons can increase the chance of seeing an apparently unusual result by chance. The registry record lists numerous secondary outcomes but does not report a multiplicity adjustment strategy or a detailed analysis plan. This means the secondary comparisons are useful descriptively, while claims based on any one of them require caution. No additional conclusions about clinical outcomes can be drawn from these antibody endpoints alone.

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

• Number of Seroconverted Subjects for Haemagglutination Inhibition (HI) Antibodies Against the A/Turkey/Turkey/1/2005 (A/Turkey) Virus Strain.
• Haemagglutination Inhibition (HI) Antibody Titers Against the A/Turkey Virus Strain.
• Number of Seroprotected Subjects for Haemagglutination Inhibition (HI) Antibodies Against the A/Turkey/Turkey/1/2005 (A/Turkey) Virus Strain.
• Number of Seroprotected Subjects for Haemagglutination Inhibition (HI) Antibodies Against the A/Turkey/Turkey/1/2005 (A/Turkey) Virus Strain.
• Number of Seroprotected Subjects for Haemagglutination Inhibition (HI) Antibodies Against the A/Turkey/Turkey/1/2005 (A/Turkey) Virus Strain.
• Geometric Mean Fold Rise (GMFR) as Regards Haemagglutination Inhibition (HI) Antibodies Against the A/Turkey/Turkey/1/2005 (A/Turkey) Virus Strain
• Geometric Mean Fold Rise (GMFR) as Regards Haemagglutination Inhibition (HI) Antibodies Against the A/Turkey/Turkey/1/2005 (A/Turkey) Virus Strain
• Number of Seroconverted Subjects for Haemagglutination Inhibition (HI) Antibodies Against the A/Turkey/Turkey/1/2005 (A/Turkey) Virus Strain.

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference represent?

A risk difference is the difference between the proportions meeting an outcome definition in two groups. It is expressed on the proportion scale: zero corresponds to equal observed proportions, positive estimates indicate a higher observed proportion in the comparison group, and negative estimates indicate a lower observed proportion. For the primary result, the posted risk differences compare each listed A/Indonesia-primed, placebo-at-Day-182 group with the A/Indonesia-primed formulation 3 group. The risk difference describes the observed contrast; it does not by itself establish causation or clinical importance.

How should a confidence interval be read?

A confidence interval communicates uncertainty around an estimate under the method used to construct it. Wider intervals indicate less precision, while narrower intervals indicate greater precision. For a risk difference, an interval including zero is compatible with no difference under the interval’s assumptions, as well as with values on either side of zero if those values lie within its limits. The primary intervals all include zero. This does not prove the groups are identical; it means the posted data do not pinpoint the difference precisely enough to exclude zero using those intervals.

What does the p-value add?

The unadjusted p-value summarizes how compatible the observed data are with a null model of no group difference, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor does it measure the size or importance of an effect. The p-values listed with these comparisons are unadjusted. The registry record does not report whether or how the analyses accounted for the several outcomes, groups, and assessment times, so the p-values should not be treated as if multiplicity adjustment had been applied.

Why distinguish counts from proportions?

The endpoint is recorded as a number of subjects meeting the seroconversion definition, alongside the number analyzed in each group. A count alone can be difficult to compare when group denominators differ. The posted proportion and risk difference put the counts in a common scale for comparison. No additional totals or recalculated rates are needed to interpret the posted estimates: the count, group denominator, proportion, and contrast each answer a different descriptive question.

Why does the analysis population matter?

The primary outcome was analyzed in the According-to-Protocol cohort for immunogenicity, defined around evaluability and availability of the specified HI measurements. This differs conceptually from an analysis of every randomized subject, because subjects without qualifying measurements or who did not meet the cohort criteria may not contribute to the stated endpoint analysis. The exact exclusions and missing-measurement handling are not reported in the registry record. Consequently, the estimates characterize the analyzed cohort and should not automatically be assumed to describe every enrolled subject.

What do secondary analyses contribute?

Secondary outcomes can examine related antibody measures, such as seroprotection, seroconversion at another assessment time, or antibody titers. Each outcome may use a different definition, timepoint, or analyzed population. This can provide broader descriptive context, but it also creates more opportunities for apparently notable differences to arise by chance when many comparisons are made. The registry record lists secondary outcomes but does not report their analysis procedures or multiplicity strategy. Their unadjusted estimates are therefore best read as supporting or exploratory evidence, not as independent confirmation of a primary finding.

What is not known about the statistical plan?

The registry record does not report the original sample-size justification, planned primary analysis model, interim analyses, or detailed missing-data procedures. It also does not list reported analyses for the secondary outcomes. General statistical principles can explain the posted measures, but they cannot fill those gaps. In particular, the planning illustrations based on observed effects are separate from the trial’s original design and do not reveal what assumptions the investigators used when planning enrollment.

11. Confidence Intervals and Precision

The primary risk-difference intervals are broad enough to include zero in all three comparisons. For formulation 1, the estimate is 0.076 and the interval extends from -0.017 to 0.168. For formulation 4, the estimate is 0.057 and the interval extends from -0.041 to 0.155. For formulation 2, the estimate is 0.047 and the interval extends from -0.055 to 0.149. Each interval also includes positive values larger than its point estimate, reflecting uncertainty in the magnitude of the contrast.

The point estimates alone can make the differences appear more settled than the data warrant. The interval limits show that the observations are compatible with a range of effects, including no difference and, for these comparisons, values on either side of zero. The intervals do not establish equivalence: a conclusion of equivalence would require a suitable prespecified margin and analysis, neither of which is reported in the registry record.

Secondary comparisons also vary in precision. At Day 224, the formulation 2 versus reference seroprotection interval includes zero, while the naïve group contrast has an interval entirely below zero. The Day 591 seroconversion intervals listed for the other primed groups include zero. These distinctions describe the reported uncertainty for those separate comparisons and do not replace the primary endpoint assessment.

Confidence intervals reflect sampling uncertainty under their statistical assumptions; they do not account automatically for bias, missing data, differences in implementation, or the consequences of choosing among many comparisons. The registry record does not provide enough detail to assess those issues fully. Interpreting the estimates together with their intervals, analysis population, and unadjusted status is more informative than treating any point estimate or p-value as decisive.

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 table gives planning illustrations in participants per arm for 80% and 90% power. The assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect for the corresponding comparison. These are planning calculations based on observed effects, not the original design assumptions for this trial; the trial’s original sample-size justification is not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm needed for an analysis to have an 80% chance of detecting the assumed effect under the calculation’s conditions, if that effect is real. The 90% column uses a higher target chance of detection and therefore generally requires more participants per arm. These are conditional design quantities, not guarantees about what a future study will find.

Rows for smaller assumed effects require more participants because a smaller contrast is harder to distinguish from random variation. For example, the rows labeled planning for 75% or 50% of the observed effect use progressively smaller effects than the row based on 100% of the observed effect; their participant requirements increase accordingly. The displayed curve should be read in the same planning context, as a depiction of how the estimated requirement changes with the assumed effect, not as a result observed in this trial.

This is not observed power. It does not describe the probability that the completed trial detected an effect after seeing its results, and it is not evidence that a result is true or false. The original allocation, analysis choices, and design assumptions may differ from the illustrative assumptions used for these calculations.

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 = 0.855; treatment proportion p₁ = 0.931; average p̄ = 0.893.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4367 = 0.8560.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4335 = 0.3648.
4. n = (0.8560 + 0.3648)² / (0.0756)² = 260.7, rounded up to 261 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 <- 0.855421686746988                          # control proportion
p1 <- 0.931034482758621                          # 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(719043)
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 = 261 (80% power), 349 (90% power)
 75% of observed effect: n per arm = 501 (80% power), 670 (90% power)
 50% of observed effect: n per arm = 1,206 (80% power), 1,614 (90% power)
power.prop.test: 260.7 
Simulated power at n = 261 per arm: 0.808 (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. Multiplicity, Missing Data and Analysis Populations

The registry record lists 32 outcome measures and 21 posted secondary outcomes, with several antibody outcomes assessed at different times. The reported results include multiple groups and comparisons. When many outcomes or contrasts are examined, the chance of at least one result appearing notable by chance can increase. Statistical approaches such as prespecified outcome hierarchies or multiplicity adjustments can address aspects of this issue, but the registry record does not report whether such procedures were planned or used.

The listed p-values for the comparisons are unadjusted. They should be read as individual comparison summaries, not as multiplicity-controlled evidence across the full set of outcomes. The record does not report a primary-versus-secondary testing sequence, family-wise error control, or a false-discovery procedure. It also does not report interim analyses, so their presence or absence cannot be determined from the registry record.

The primary population is defined as the According-to-Protocol cohort for immunogenicity, consisting of evaluable subjects with at least Day 182 and Day 192 or Day 549 and Day 559 HI results. The posted description does not give a full account of how many subjects were excluded from each outcome analysis, why measurements were unavailable, or how missing observations were handled. It does not report an intention-to-treat analysis for this endpoint or sensitivity analyses addressing missing data.

These omissions matter because the observed comparison is conditional on the analyzed population and the available measurements. If missingness or protocol deviations were related to response, the analyzed cohort might differ from the randomized groups in ways that affect interpretation. That possibility cannot be quantified from the registry record. The cautious reading is to describe the posted cohort-specific estimates, acknowledge that multiplicity and missing-data methods are not reported, and avoid inferring that unreported procedures were performed.

15. 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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cerebrovascular accident (1.7%), nephrolithiasis (1.6%), breast cancer (0.8%), pneumonia (0.8%), appendicitis (0.8%).

The safety record gives, by group, numbers at risk and numbers affected for serious events and other events. For serious events, the listed affected counts range from 9 to 15 across the groups, with the corresponding at-risk figures listed from 119 to 122. These are group-level registry counts; they should be read alongside their own denominators rather than compared as bare counts. The record also lists serious-event terms and percentages, including cerebrovascular accident at 1.7%, nephrolithiasis at 1.6%, and breast cancer, pneumonia, appendicitis, and pancreatitis at 0.8% each.

The registry record does not report deaths in the safety summary. The displayed adverse-event information does not by itself establish whether an event was caused by vaccination, and it does not provide a complete basis for comparing safety between schedules. Interpretation depends on definitions, follow-up, exposure, and ascertainment details, some of which are not reported in the registry record. These figures describe recorded events; they are not a recommendation or a conclusion about an individual’s risk.

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

The posted results describe HI antibody responses in the analyzed groups at specified assessment times. On the primary Day 559 seroconversion endpoint, the three comparison groups each had a higher observed proportion than the listed reference group, but all three risk-difference confidence intervals include zero. The estimates are therefore uncertain, and the registry results do not establish a clear difference between these groups on that endpoint.

The secondary outcomes broaden the description of antibody response. Their pattern is not uniform across outcomes and times: most of the listed secondary comparisons have intervals including zero, while one Day 224 seroprotection comparison has an interval below zero for the naïve group contrast. That finding concerns a different comparison and timepoint. Because the secondary results are unadjusted and the multiplicity strategy is not reported, they warrant cautious interpretation.

These outcomes concern antibody measurements, not confirmed influenza illness, hospitalization, or other clinical events. The registry record does not report a clinical efficacy endpoint establishing how the measured antibody responses relate to protection against influenza. A seroconversion or seroprotection result should not be treated as proof of clinical benefit. Nor does an interval including zero prove that two schedules are equivalent.

The trial’s randomized, double-masked, parallel design is relevant context, but the registry record does not provide all details needed to assess conduct, analysis, missing observations, or potential bias. The reported estimates apply to the stated outcome populations and comparisons. They do not automatically generalize beyond those groups or resolve the uncertainty that remains around the primary contrast.

Overall, the most defensible interpretation is descriptive: the record reports high observed seroconversion proportions in the primary analysis groups, with imprecise between-group differences. The safety listings are also descriptive and do not assign causality. No medical decision should be based on these statistical summaries alone.

17. Why This Trial Matters Statistically

This trial illustrates why outcome definitions and timing matter in immunogenicity studies. The primary endpoint is not simply an antibody value: it is a subject-level classification based on prespecified pre- and post-vaccination titer criteria. The timing is explicit, with Day 549 serving as the pre-vaccination reference for the Day 559 result. Related secondary outcomes at other times answer different questions and should not be collapsed into a single overall claim.

The example also shows the value of reporting effects with uncertainty. The primary point estimates are positive, but their intervals extend across zero. This distinction prevents a reader from treating a directional point estimate as definitive evidence. Counts, denominators, proportions, risk differences, confidence intervals, and unadjusted p-values each contribute different information and are most useful when read together.

Another statistical issue is the distinction between planned sample size and observed evidence. The planning illustrations use effects derived from the observed comparisons and explicit calculation assumptions. They show how much larger a future study might need to be to detect a smaller assumed difference, but they do not tell whether the completed trial was adequately planned. The original sample-size justification is not reported in the registry record.

Finally, the record brings attention to multiplicity and analysis populations. Many related outcomes and timepoints can generate a complex evidence pattern, while an according-to-protocol cohort may differ from all randomized participants. Without reported adjustment, missing-data procedures, or a full statistical plan, secondary findings and cohort-specific estimates need careful qualification. These are broadly useful lessons for reading clinical trial registries: define the estimand, check the analyzed population, inspect precision, and distinguish antibody outcomes from clinical outcomes.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record leaves several trial-specific details unreported. It does not give the original sample-size justification, so the enrollment cannot be interpreted as evidence that the study was designed around a particular effect size or power target. The separate planning illustrations are not a substitute for that missing design rationale.

The primary analysis is described for an According-to-Protocol immunogenicity cohort, but the record does not provide a complete account of exclusions, protocol deviations, outcome-specific denominators beyond the posted comparisons, or missing-data handling. The effect estimates therefore describe the analyzed subjects, and the extent to which they represent all randomized or enrolled subjects cannot be established from the registry information alone.

The trial studied several formulations, schedules, outcomes, and assessment times. The registry record does not report a detailed multiplicity strategy, adjusted secondary analyses, or interim-analysis information. The listed p-values are unadjusted, which limits the strength of conclusions drawn from individual secondary comparisons.

The primary endpoint is an antibody response measure rather than a clinical influenza outcome. The record does not report a clinical endpoint or a relationship between the antibody definition and clinical protection. The safety summary provides group counts and selected event terms, but deaths are not reported in the record and event causality is not established by these listings.

Finally, the arm descriptions in the registry record are not complete for every schedule. The statistical comparisons can be interpreted as the named groups and endpoint definitions specify, but details beyond those descriptions should not be inferred. These limitations constrain conclusions about generalizability, causal interpretation of individual safety events, and the clinical meaning of measured antibody responses.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Immunogenicity & Safety of GSK's Avian Flu Vaccine 1557484A Given to Adults Aged ≥18 Years — NCT00719043.
• Registry record last updated 2018-07-09; status last verified 2018-05.
• Results first posted 2014-02-07.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

This completed Phase 2 registry record describes a randomized, double-masked, parallel-group trial of monovalent H5N1 vaccine in adults aged at least 18 years. Enrollment was 841, and GlaxoSmithKline was the sponsor. The primary outcome was the number of subjects seroconverted for HI antibodies against the A/Turkey/Turkey/1/2005 strain at Day 559, using Day 549 as the pre-vaccination reference.

The primary comparisons show positive estimated risk differences for the three listed groups relative to the reference, but every confidence interval includes zero. Secondary outcomes examine related antibody measures at other times and show a mixed pattern; their listed comparisons are unadjusted. Safety information includes serious and other event counts by group and selected serious-event terms.

The registry record does not report the original sample-size justification, detailed multiplicity or missing-data procedures, or a clinical influenza endpoint. The findings are best understood as uncertain, cohort-specific antibody-response comparisons and descriptive safety listings, not as proof of clinical protection or as a complete account of the trial’s statistical plan.