Study of Malaria Vaccine RTS,S/AS01E in Plasmodium Falciparum-infected and Uninfected Adults Pre-treated With Anti-malarial Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Malaria Vaccine RTS,S/AS01E in Plasmodium Falciparum-infected and Uninfected Adults Pre-treated With Anti-malarial Therapy (NCT04661579), a randomized phase 2 study. The primary outcome is Time to First PCR-detectable Malaria Infection During the Active Detection of Infection (ADI) Phase in Groups 1 and 4.

2. Clinical Question

The registry describes a study intended to assess vaccine efficacy after parasite clearance in adults who were positive for P. falciparum at the start. Its stated rationale was to address reduced vaccine responsiveness reported in actively or chronically infected adults. The trial also included groups without detectable parasitemia at baseline and a parasitemic vaccine group without anti-malarial treatment. Those groups do not define the primary comparison.

The primary question is therefore narrower than whether vaccination prevents malaria generally. It concerns the comparison of vaccine and rabies vaccine in the specified treated, parasitemic groups during a defined period of active infection detection. The endpoint relies on PCR detection, which the registry describes as capable of detecting sub-clinical parasitemia. It does not, by itself, establish the clinical severity or symptomatic nature of an infection.

3. Trial Design

This was a Phase 2b randomized, open-label, controlled, single-center study in Kenya, described in the registry as a phase 2 study with parallel groups and no masking. The registry records enrollment of 620 and a completed study status. The recorded start date is 2020-11-06 and the primary completion date is 2022-06-22. These are registry dates, not evidence about the duration of follow-up for each participant.

The five groups varied by baseline parasitemia, anti-malarial treatment or prophylaxis, and vaccine assignment. For the primary comparison, Group 1 included participants with detectable baseline parasitemia who received dihydroartemisinin-piperaquine plus low dose primaquine before RTS,S/AS01E vaccination. Group 4 included participants with detectable baseline parasitemia who received the described anti-malarial treatment before rabies vaccination. The posted primary outcome data give 151 participants for each of these groups.

The vaccine groups also included participants without detectable baseline parasitemia who received anti-malarial prophylaxis, and a smaller group of parasitemic participants who did not receive anti-malarial medication to clear parasites. The registry describes RTS,S/AS01E vaccination on a 0, 1, and 7 month schedule in the untreated parasitemic group. Some other group descriptions are incomplete in the registry record, so their full schedules should not be inferred from the abbreviated text.

Active detection of infection began 2 weeks after the third vaccination, approximately week 30, and continued for up to 35 weeks. Participants had blood samples collected every 21 days during that phase for PCR assays. The registry identifies the according-to-protocol efficacy cohort for the primary endpoint, but the full cohort definition is not available in the record. The original design rationale, allocation details beyond randomization, and trial-specific sample-size assumptions 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: Participants were stratified by baseline P. falciparum parasitemia status and then block randomized. The first 105 participants who were positive for parasitemia at baseline were randomized in a 1:1:1 ratio with 35 participants assigned to each of Groups 1, 3 and 4. The next 258 participants with baseline parasitemia were randomized in a 1:1 ratio to Groups 1 and 4. Participants who were negative for parasitemia at baseline were randomized in a 1:1 ratio to Groups 2 and 5.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The primary endpoint was pre-specified to be analyzed in Groups 1 and 4 only. The According to Protocol (ATP) cohort for efficacy includes all participants in the TVC with no major protocol deviations that could potentially interfere with the efficacy assessment of the study vaccine and who contributed to the time at risk starting 14 days after the third dose.

5. Baseline Characteristics

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

Population: The total vaccinated cohort (TVC) includes all randomized participants who received at least one vaccination.

6. Primary Endpoint

The registry lists the primary outcome as Time to First PCR-detectable Malaria Infection During the Active Detection of Infection (ADI) Phase in Groups 1 and 4, measured over The active detection of infection phase began 2 weeks after the third vaccination (approximately week 30) for up to 35 weeks. Participants provided blood samples every 21 days during the ADI phase for PCR assays..

The primary endpoint is the rate of first PCR-detectable malaria infection during the active detection of infection phase, reported as events per person year at risk. A positive PCR result from blood collected during that phase was recorded as an event for P. falciparum blood-stage infection. The registry describes use of a sensitive PCR assay intended to detect sub-clinical parasitemia, so the endpoint captures laboratory-detected infection and is not limited to illness that prompted a clinical visit.

Expressing the outcome as a rate relates the number of first infection events to the time participants were at risk. This can be useful when participants contribute different amounts of observation time or when follow-up ends at an event. A rate is not the same as the proportion of participants who became infected: it incorporates exposure time in its denominator. The registry reports the rates as 1.01 events per person year at risk in Group 1 and 1.49 in Group 4.

The endpoint is focused on time to first PCR-detectable infection, rather than recurrent infections or clinical malaria episodes. The registry’s description says that rate is calculated over time elapsed until the first event. Details of the handling of participants with incomplete observation, including censoring rules, are not reported in the registry record. Accordingly, interpretation should remain tied to the defined PCR-detection phase and the reported rate measure rather than extending to other malaria outcomes.

7. Results Posted in the Registry

• Group 4: Positive Parasitemia; Anti-malarial Treatment + Rabies Vaccine: 1.49 versus 1.01 (Events per person year at risk) on control; rate ratio 1.48 (95% CI 0.52–4.22, approximate, Poisson model); p ≈ 0.468.

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.

Time to First PCR-detectable Malaria Infection During the Active Detection of Infection Phase in Groups 2 and 5

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • Group 5: No Parasitemia, Anti-malarial Prophylaxis + Rabies Vaccine: 0.62 versus 0.77 (Events per person year at risk) on control; rate ratio 0.81 (95% CI 0.17–3.81, approximate, Poisson model); p ≈ 0.785.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Group 5: No Parasitemia, Anti-malarial Prophylaxis + Rabies Vaccine and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning PCR-detected malaria infection, adverse events, and antibody responses. A second malaria-rate comparison concerns participants without baseline parasitemia who received anti-malarial prophylaxis and were assigned RTS,S/AS01E or rabies vaccine. Its re-calculated interval is broad, and the sponsor-reported efficacy analysis is also uncertain. This secondary comparison does not provide a clear, precise complement to the primary result.

The other listed secondary outcomes concern serious adverse events, solicited and unsolicited adverse events, circumsporozoite antibody titers and avidity, and hepatitis B surface antigen antibody titers. Their outcome titles identify different aspects of safety and immune response; they are not substitutes for the primary PCR-detected infection endpoint. Results for these measures are not reported in the registry record in the information summarized for this analysis. Their direction or magnitude should not be inferred from the outcome titles or from the malaria comparison.

Secondary findings generally carry less weight than the prespecified primary comparison when many outcomes are examined. General statistical explanation: testing multiple hypotheses increases the chance that at least one result appears unusual by chance, unless the analysis plan accounts for multiplicity. The registry record does not report a multiplicity adjustment or a hierarchy governing interpretation of secondary outcomes. Therefore, any unadjusted secondary p-values should be treated as exploratory rather than as stand-alone confirmation. This caution does not imply that secondary outcomes are unimportant; it reflects the additional uncertainty created by multiple comparisons and the absence of a reported adjustment plan.

The record lists seven secondary outcomes and reports an analysis for the secondary malaria comparison. It does not support a comprehensive conclusion across every safety or immunogenicity outcome. In particular, the available secondary analyses cannot establish a general pattern of vaccine effect across different outcome types or groups.

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

• Time to First PCR-detectable Malaria Infection During the Active Detection of Infection Phase in Groups 2 and 5
• Number of Participants With Serious Adverse Events (SAEs)
• Number of Participants With Solicited Local and Systemic Adverse Events (AEs)
• Number of Participants With Unsolicited Adverse Events
• Geometric Mean Titer of Anti-Plasmodium Falciparum Circumsporozoite (CS) Antibodies in Groups 1, 2, and 3
• Anti-Plasmodium Falciparum Circumsporozoite (CS) Antibody Avidity Index in Groups 1, 2, and 3
• Geometric Mean Titer (GMT) of Anti-Hepatitis B Surface Antigen (HBsAg) Antibodies in Groups 1, 2, and 3

9. Statistical Interpretation

10. Statistical Methods Explained

What does an event rate represent?

General statistical explanation: an event rate relates observed events to the amount of time participants contribute while at risk. It differs from a risk or proportion, which asks what share of participants experienced an event over a defined period. Rates are often useful when follow-up time varies, but their interpretation depends on how at-risk time and event follow-up are defined. The registry presents the primary endpoint in events per person year at risk and describes the event as a positive PCR result for P. falciparum during active detection.

The posted primary rates are 1.01 for the RTS,S/AS01E group and 1.49 for the rabies vaccine group. The re-calculation compares these using a rate ratio, with Group 4 as the comparison group relative to Group 1. The reported ratio is 1.475. A rate ratio of this kind expresses a relative rate contrast; it is not an absolute difference in infections and should not be read as the percentage of participants infected.

Why use a rate ratio?

General statistical explanation: a rate ratio places two event rates on a relative scale. A value near 1 represents similar estimated rates; values on either side indicate the direction of the estimated relative contrast according to the numerator and denominator order. The registry’s comparison labels the estimate as a rate ratio. It does not report a confidence interval for the individual arm rates, and no additional arm-level precision measure should be inferred.

The re-calculated comparison uses a Poisson approach. General statistical explanation: a Poisson model is commonly used for event counts when the amount of exposure time is accounted for. The model relies on assumptions about the event process and its variability. If events vary more than the Poisson model allows, a method that accounts for over-dispersion may be needed; over-dispersion means the observed variability exceeds the model’s expected variability. The registry record does not report a dispersion estimate or a diagnostic assessment, so whether over-dispersion was examined is not reported in the registry record.

What does the interval communicate?

The re-calculated primary rate ratio has a reported interval from 0.516 to 4.216. General statistical explanation: a confidence interval describes the range of estimates compatible with the data and the calculation’s assumptions at its stated confidence level. A wide interval signals limited precision. If it spans the null value for a rate ratio, the data do not sharply distinguish the groups under that analysis. The re-calculated interval is not the same as a sponsor-reported efficacy interval, because the two analyses use different measures and may use different methods.

The re-calculated p-value is 0.468. General statistical explanation: a p-value measures how unusual data at least as incompatible with a specified null model would be, if that model and its assumptions were correct. It is not the probability that the null hypothesis is true, nor a measure of clinical importance. Its interpretation also depends on the analysis being considered. The posted sponsor analysis uses a Wald test and reports vaccine efficacy; the re-calculation is an unadjusted comparison based on posted summary rates. These should remain clearly distinguished.

Why might analyses differ?

The record reports a sponsor analysis of vaccine efficacy and a separate rate-ratio re-calculation from summary statistics. Differences can arise when analyses use different estimands, populations, adjustments, event-time definitions, or statistical methods. This is a general explanation, not a claim about which difference occurred in this trial: the record does not give enough information to identify the reason for the discrepancy. The specified according-to-protocol cohort, details of the sponsor’s full model, and the precise conversion between its efficacy measure and the posted rate data are not reported in the registry record.

The sponsor analysis reports a Wald test, vaccine efficacy of 35.9, a 95% confidence interval from 10.3 to 54.2, and p = 0.009. In view of the flagged discrepancy, that analysis takes precedence over the simple re-calculation. The re-calculation is best treated as a transparent check of the posted summary rates, not a replacement for the trial’s own analysis.

What does randomization contribute?

General statistical explanation: random assignment is intended to make treatment groups comparable, on average, with respect to measured and unmeasured baseline factors. It does not guarantee balance in a particular trial, especially within a restricted analysis population, and it does not resolve missing-data, adherence, or outcome-measurement concerns. This study was open-label, so participants and study personnel were not masked according to the registry. PCR-based outcome assessment is laboratory-based, but the record does not describe laboratory masking or other safeguards against assessment bias.

The primary endpoint was specified for Groups 1 and 4, and the registry describes an according-to-protocol efficacy cohort. Such a cohort can differ from an analysis of all randomized participants if eligibility for analysis depends on protocol deviations or contribution to efficacy follow-up. The complete cohort rules and the number excluded from that analysis are not reported in the registry record. The posted primary arm counts are 151 and 151, but those figures alone do not establish how every randomized participant was handled.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimate, not whether an estimate is important. The unadjusted primary rate ratio is 1.475, with a reported interval from 0.516 to 4.216. The breadth of this interval means that the summary data do not yield a narrowly estimated relative rate. Its range includes values on either side of the null value of 1 for a rate ratio, so the re-calculation does not isolate a single direction of association with high precision.

The sponsor’s analysis reports vaccine efficacy of 35.9, with a 95% confidence interval from 10.3 to 54.2. This interval belongs to the sponsor-reported efficacy analysis, not the rate-ratio re-calculation. The registry flags a discrepancy between analyses; consequently, the sponsor analysis takes precedence, and the distinct estimates and intervals should not be merged. The record does not give details sufficient to explain why the results differ.

The secondary re-calculated rate ratio is 0.805, with a reported interval from 0.170 to 3.812. It too is imprecise, as reflected by the wide interval. The sponsor’s corresponding efficacy result is reported separately with its own interval, from -97 to 22.2. Neither interval should be read as a range containing a fixed proportion of individual participant outcomes. General statistical explanation: a confidence interval is a measure of uncertainty about an estimated parameter under a specified method and its assumptions; it is not a prediction interval for individual outcomes.

There are no posted confidence intervals for the individual primary arm rates in the record. The rate-ratio interval is therefore the appropriate posted uncertainty measure for the re-calculated contrast, while the sponsor efficacy interval describes its own analysis. The trial’s sample size and the width of an interval do not establish whether an effect is clinically meaningful; that judgment requires a prespecified interpretation framework, which is not reported in the registry record.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

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

For the primary comparison, the illustration lists 2,251 participants per arm for planning for 100% of the observed effect, 4,166 for planning for 75% of the observed effect, and 9,781 for planning for 50% of the observed effect at 80% power. The corresponding 90% power figures are 3,013, 5,576, and 13,094 participants per arm. For the secondary comparison, the listed figures are 12,701, 21,919, and 47,912 participants per arm for 80% power, and 17,003, 29,343, and 64,141 participants per arm for 90% power, at the same stated effect fractions.

In plain language, the 80% power column describes a planning scenario intended to give an 80% chance of detecting the specified effect under the stated assumptions if that effect is real; the 90% column describes the analogous 90% planning target. Higher power targets generally require more participants under the same assumptions. Detecting a smaller effect also requires more participants, as reflected by the figures for smaller fractions of the observed effect. These are not observed power figures, and they do not show what power the completed trial actually had.

The planning description states that time-to-event tables give total events using the Schoenfeld method and all other tables give participants per arm. These outcomes are event rates, so the listed figures are participants per arm, not total events. The trial’s actual enrollment was 620; the planning illustrations are not a retrospective statement that the trial should have enrolled a particular number.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 1.0100; treatment rate λ₁ = 1.4900 events per patient-year; follow-up T = 0.04 years.
2. n = (1.96 + 0.842)² × (1/1.0100 + 1/1.4900) / (0.04 × [ln(1.475)]²) = 2,250.1, rounded up to 2,251 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
lambda0 <- 1.01                      # control rate, events per patient-year
lambda1 <- 1.49                      # treatment rate
tt      <- 0.0383288616328095                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(4661579)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 2,251 (80% power), 3,013 (90% power)
 75% of observed effect: n per arm = 4,166 (80% power), 5,576 (90% power)
 50% of observed effect: n per arm = 9,781 (80% power), 13,094 (90% power)
Simulated power, Poisson counts, n = 2,251 per arm: 0.806
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.634

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as a Wald test of vaccine efficacy: 35.9, with a 95% confidence interval from 10.3 to 54.2 and p = 0.009. Separately, the simple unadjusted re-calculation from the posted arm rates gives a rate ratio of 1.475, with an interval from 0.516 to 4.216 and p = 0.468. Because the registry flags a discrepancy, the sponsor’s own analysis takes precedence.

These results are not alternate formats of one estimate that can be substituted without qualification. Vaccine efficacy and a rate ratio are different measures, and the registry does not provide the analysis details needed to reconcile them. It does not establish whether the discrepancy reflects the analysis population, an adjustment, an endpoint implementation, or another methodological difference. Those explanations should not be presumed.

The re-calculation is an unadjusted check based on posted summary rates and a Poisson approach. It can help readers understand the rough contrast implied by those summaries, but it cannot reproduce an analysis whose model and population details are not fully reported. The sponsor-reported result should therefore be the primary reference for the trial’s own efficacy finding, while the re-calculation remains a distinct, less authoritative analysis of the posted summaries.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and specifies that its main efficacy analysis applies to Groups 1 and 4. It also lists secondary outcomes and reports an additional malaria comparison. However, a complete statistical analysis plan, including the prespecified testing hierarchy and any multiplicity adjustment, is not reported in the registry record. Without that information, it is unclear whether the reported secondary analyses were confirmatory, exploratory, or part of a broader testing strategy.

General statistical explanation: when researchers test multiple outcomes or contrasts, the chance of at least one small p-value under null effects can increase. Adjustments or a prespecified hierarchy can help control how such findings are interpreted. No adjustment method is reported in the registry record, so secondary p-values should not be interpreted as though they necessarily account for all analyses conducted. The record’s count of posted analyses does not establish how many analyses were planned or performed.

The primary population is described as an according-to-protocol efficacy cohort drawn from the total vaccinated cohort, excluding participants with major protocol deviations that could interfere with vaccine efficacy assessment and requiring contribution to efficacy assessment. The full definition is truncated in the registry record. The numbers screened, randomized, excluded from the efficacy population, or analyzed under other population definitions are not fully described in the information available for this analysis. The posted endpoint arm counts should not be treated as a complete participant flow.

Methods for missing PCR samples, missed visits, withdrawal, censoring, and incomplete follow-up are not reported in the registry record. Nor is it clear how deviations from the sampling schedule affected person-time or endpoint classification. These details matter for a rate endpoint because the estimate depends on both event ascertainment and time at risk. The registry also does not report interim analyses, stopping rules, or the trial’s original sample-size justification. These absences limit assessment of the analysis framework; they do not establish that a particular method was or was not used.

16. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: abortion spontaneous (2.9%), malaria (0.8%), pneumonia (0.8%), prostatic haemorrhage (0.8%), haemorrhoids (0.8%).

The registry posts serious adverse event counts by group, with the number at risk for each group. Group 1 had 3 serious adverse events among 160 participants at risk; Group 2 had 2 among 124; Group 3 had 1 among 35; Group 4 had 1 among 159; and Group 5 had 3 among 127. The registry also records 1 death in Group 1 and none in the other listed groups. These are group-specific counts and denominators, not estimates adjusted for follow-up time or baseline differences.

Serious adverse events are not interchangeable with all adverse events. The record separately reports other adverse events affecting 111 of 160 at risk in Group 1, 96 of 124 in Group 2, 25 of 35 in Group 3, 110 of 159 in Group 4, and 92 of 127 in Group 5. These broad counts do not establish cause, severity beyond the recorded category, or a treatment-related difference. The registry’s listed serious-event terms include spontaneous abortion, malaria, pneumonia, prostatic haemorrhage, haemorrhoids, and strangulated inguinal hernia, with the percentages recorded in the registry.

These figures are descriptive. The registry record does not provide a comparative safety model, uncertainty intervals for between-group differences, or enough information to attribute events to a study intervention. The counts should not be interpreted as proof of a safety difference or absence of one.

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

The posted primary data describe PCR-detected first infection rates during an active surveillance phase in two groups of adults with detectable baseline parasitemia who received anti-malarial treatment before vaccination. The sponsor’s reported efficacy analysis is 35.9, with a 95% confidence interval from 10.3 to 54.2 and p = 0.009. The registry flags a discrepancy with the simple unadjusted re-calculation, so the sponsor analysis takes precedence when describing the trial’s own result.

The record does not establish that the sponsor estimate applies to every participant or to every malaria outcome. The primary endpoint was limited to the specified groups and to PCR-detectable infection during the defined active detection phase. It does not directly measure symptomatic malaria, severe disease, recurrent infection, or outcomes after the surveillance period. The result also should not be generalized automatically to people outside the trial’s adult population, setting, treatment regimen, or eligibility conditions.

The re-calculated rate ratio has a wide interval, and the secondary malaria comparison is also imprecise. These uncertainties are relevant even though the sponsor’s primary analysis reports a statistically significant result. Statistical significance does not quantify the clinical importance of an effect, establish its durability, or resolve the discrepancy between analysis approaches.

The record also does not report the full analysis plan, methods for missing observations, or complete efficacy-cohort definition. These omissions constrain independent appraisal. The data therefore support a focused account of the registry’s posted analyses, not a broad conclusion that the vaccine does or does not prevent malaria in all settings. No treatment decision should be inferred from these statistical summaries alone.

18. Why This Trial Matters Statistically

This trial is statistically interesting because it asks about vaccine performance in a population with detectable P. falciparum at baseline, after anti-malarial treatment, rather than treating baseline infection as an incidental characteristic. The primary comparison isolates the groups described as parasitemic at baseline and treated before receiving either RTS,S/AS01E or rabies vaccine. That makes the endpoint and analysis population central to interpreting the result.

The primary outcome is a PCR-based rate of first infection, not a conventional proportion with clinical disease. It connects infection events to person-time at risk and uses repeated laboratory surveillance during a defined phase. That design highlights familiar statistical questions about event rates, time at risk, and the precision of relative comparisons. The posted re-calculation illustrates how summary rates can be compared, while the discrepancy with the sponsor analysis shows why a simple calculation cannot replace a trial’s complete analysis.

It also demonstrates why registry results need to be read with attention to outcome definitions and analysis populations. An according-to-protocol cohort, a specified set of groups, and a particular surveillance period define the scope of the estimate. An endpoint based on sub-clinical PCR detection is not automatically equivalent to clinically apparent malaria.

Finally, the trial makes the distinction between estimation and planning visible. The planning illustrations use the observed effects under stated assumptions, whereas the original design justification is not reported. Such illustrations can describe how assumed effects and power targets relate to enrollment needs, but they cannot establish the design choices made before the trial. Together, these issues make the record a useful case for examining estimand, uncertainty, reproducibility, and careful limits on inference.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

Several limitations are specific to interpreting this record. First, it is open-label, and the registry does not state whether laboratory personnel assessing PCR samples were masked. PCR is an objective laboratory measure, but details of sample handling, assay validation in this study, and assessment safeguards are not reported in the registry record.

Second, the outcome depends on scheduled sampling every 21 days during active detection. The record does not state how missed samples, delayed visits, or incomplete follow-up were handled, or how at-risk time was calculated when observation ended. These omissions complicate independent evaluation of the rate estimate and possible differences in ascertainment.

Third, the primary efficacy cohort is described only partially. The according-to-protocol definition is truncated, and participant flow into that cohort is not fully available. The group counts in the outcome record therefore should not be assumed to represent every randomized participant. The record also does not give a full account of adherence, protocol deviations, or exclusions.

Fourth, there is a flagged difference between the sponsor-reported efficacy analysis and the unadjusted rate re-calculation. The registry does not explain the source of the difference or provide the full model details needed for reconciliation. The sponsor result takes precedence, but the discrepancy limits independent replication from the summary data alone.

Finally, the study is described as single center and concerns a specific adult population, treatment schedule, and surveillance period. Results should not be extended without evidence to other populations, settings, vaccine schedules, or clinical endpoints. The original sample-size rationale, multiplicity plan, missing-data methods, and interim-analysis details are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Malaria Vaccine RTS,S/AS01E in Plasmodium Falciparum-infected and Uninfected Adults Pre-treated With Anti-malarial Therapy — NCT04661579.
• Registry record last updated 2024-07-19; status last verified 2024-01.
• Results first posted 2024-07-19.
• 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

The registry describes a completed, randomized, open-label, controlled, single-center Phase 2b study in adults age 18-55 in Kenya. Enrollment was 620. The primary endpoint was the rate of first PCR-detectable malaria infection during active detection of infection in treated participants with detectable baseline parasitemia, comparing RTS,S/AS01E with rabies vaccine.

Posted primary rates were 1.01 and 1.49 events per person year at risk. The sponsor reports vaccine efficacy of 35.9, with a 95% confidence interval from 10.3 to 54.2 and p = 0.009. The registry flags a discrepancy with the unadjusted re-calculation; the sponsor’s own analysis takes precedence. The full analysis plan, original sample-size rationale, and several details of missing-data and efficacy-population handling are not reported in the registry record.