Efficacy and Safety Study of Tafenoquine (TQ) Co-administered With Dihydroartemisinin-piperaquine (DHA-PQP) for the Radical Cure of Plasmodium Vivax (P. Vivax) Malaria: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety Study of Tafenoquine (TQ) Co-administered With Dihydroartemisinin-piperaquine (DHA-PQP) for the Radical Cure of Plasmodium Vivax (P. Vivax) Malaria (NCT02802501), a randomized phase 3 study. The primary outcome is Percentage of Participants With Relapse-free Efficacy at Six Months After Administration of Tafenoquine With DHA-PQP and DHA-PQP Alone.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, parallel-group, placebo-controlled superiority study sponsored by GlaxoSmithKline. The registry describes the trial as double-blind and double-dummy; its masking designation is quadruple. DHA-PQP was open label, while matched placebos were used to mask the tafenoquine and primaquine assignments. The recorded enrollment was 150.

Three groups received DHA-PQP from Day 1 to Day 3. One group received a single 300 mg dose of tafenoquine on Day 1 and matched placebo for primaquine through Day 14. Another received primaquine 15 mg from Day 1 to Day 14 and matched placebo for tafenoquine on Day 1. The DHA-PQP-only group received matched placebos for both drugs. The outcome records contain 50 participants in each of these three groups for the posted primary and secondary comparisons.

The main comparison focused on tafenoquine plus DHA-PQP versus DHA-PQP alone. The primaquine plus DHA-PQP group was included as an informal comparison, as described in the registry. The study was conducted at a single center in male Indonesian soldiers with P. vivax malaria. Participants who experienced recurrence during the study were to receive ACT plus PQ rescue treatment, in line with the local treatment guidelines described in the registry.

The registry records the study as completed. Its listed time points include the primary efficacy assessment at 6 months post-dose, a 4-month efficacy assessment, time to relapse, time to fever clearance, time to parasite clearance, recrudescence, and adverse events. The registry record does not report the trial's original sample-size justification, detailed randomization procedures, or the full statistical analysis plan.

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: A total of 164 participants were screened of whom 14 failed during screening and 150 were randomized to receive dihydroartemisinin-piperaquine (DHA-PQP) only, tafenoquine+DHA-PQP and primaquine+DHA-PQP in a ratio of 1:1:1.

Double-blind (Up to Day 180)

Open-Label (Day 180 to Day 195)

Analysis population for the primary outcome, as defined in the registry: Microbiologic Intent-to-Treat (mITT) Population consisted of all randomized participants who received at least one dose of blinded study treatment and had microscopically confirmed P. vivax parasitamia at Baseline.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Relapse-free Efficacy at Six Months After Administration of Tafenoquine With DHA-PQP and DHA-PQP Alone, measured over 6 months post-dose.

The primary endpoint was the percentage of participants meeting the definition of relapse-free efficacy at 6 months post-dose. It was not simply a count of participants without symptoms or a single parasite test at the end of follow-up. A participant had to have non-zero P. vivax asexual parasite count at baseline, demonstrate initial clearance, and have no positive asexual parasite count at any assessment before or on Day 180 after initial clearance. Participants also had to avoid concomitant medication with antimalarial activity, other than study treatment, between Day 1 and their last parasite assessment, and be parasite-free at 6 months.

The primary endpoint was assessed in the microbiologic Intent-to-Treat population, defined as randomized participants who received at least one dose of blinded study treatment and had microscopically confirmed baseline P. vivax parasitemia. The registry reports the percentage meeting the endpoint in each group. The endpoint is relevant to the trial's stated aim because it combines initial parasite clearance with absence of recorded recurrence during the defined follow-up. Its conditions also make clear that the result depends on serial assessments and on the specified restrictions on other antimalarial medication.

As a binary endpoint, each participant either met or did not meet the full definition. That summary is useful for comparing the proportion meeting the criterion at the specified time point, but it does not by itself describe when recurrences occurred. The sponsor's reported time-to-event analysis addresses a different feature of the follow-up and should not be treated as identical to the endpoint percentage.

7. Results Posted in the Registry

• Tafenoquine+ DHA-PQP: 22.0% (11/50) versus 12.0% (6/50) on control; risk difference 10.0 percentage points (95% CI -4.6 to 24.6), risk ratio 1.83 (0.73–4.57); unadjusted two-proportion z-test p = 0.183.

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.

Percentage of Participants With Relapse-free Efficacy at Six Months After Administration of Tafenoquine With DHA-PQP and Primaquine+DHA-PQP

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Primaquine+DHA-PQP: 52.0% (26/50) versus 22.0% (11/50) on control; risk difference 30.0 percentage points (95% CI 12.0 to 48.0), risk ratio 2.36 (1.32–4.25); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Primaquine+DHA-PQP than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Relapse-free Efficacy at Six Months After Administration of Primaquine With DHA-PQP and DHA-PQP Alone

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Primaquine+DHA-PQP: 52.0% (26/50) versus 12.0% (6/50) on control; risk difference 40.0 percentage points (95% CI 23.5 to 56.5), risk ratio 4.33 (1.95–9.61); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Primaquine+DHA-PQP than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Relapse-free Efficacy at Four Months After Administration of Tafenoquine With DHA-PQP and DHA-PQP Alone

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Tafenoquine+ DHA-PQP: 28.0% (14/50) versus 16.0% (8/50) on control; risk difference 12.0 percentage points (95% CI -4.1 to 28.1), risk ratio 1.75 (0.81–3.80); unadjusted two-proportion z-test p = 0.148.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tafenoquine+ DHA-PQP and the control. The interval gives the range of effects that remain compatible with the data.

The secondary results cover efficacy at an additional follow-up point, comparisons involving the primaquine group, and other outcomes listed in the registry such as relapse timing, fever and parasite clearance, recrudescence, and adverse events. Across the posted efficacy comparisons, the general pattern is that the primaquine plus DHA-PQP group has higher six-month relapse-free endpoint proportions than the two DHA-PQP-only or tafenoquine plus DHA-PQP groups. The tafenoquine comparison with DHA-PQP alone also has a higher observed four-month proportion, while its recalculated interval includes no difference. These patterns add context but do not replace the primary comparison.

For the tafenoquine versus DHA-PQP-only comparison, the primary fixed-time summary and the sponsor's time-to-event result do not produce the same statistical conclusion. The secondary results do not resolve that methodological discrepancy. Results at another time point or involving another treatment group address related but distinct questions, and the registry describes the primaquine group as an informal comparison. They should not be taken as a direct confirmation of the primary comparison.

There are 21 secondary outcome measures posted in the registry record. Examining multiple outcomes and contrasts creates multiplicity: even when no true effect exists for any of them, a collection of tests can produce apparently notable findings by chance. The registry record does not report a multiplicity adjustment or testing hierarchy. Accordingly, unadjusted secondary results carry less inferential weight than a clearly prespecified primary analysis, particularly when the analytic details are not complete. They are useful for describing the overall pattern and identifying questions for further evaluation, but should not be presented as independent proof of efficacy or as a basis for choosing among treatments.

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

• Percentage of Participants With Relapse-free Efficacy at Six Months After Administration of Tafenoquine With DHA-PQP and Primaquine+DHA-PQP
• Percentage of Participants With Relapse-free Efficacy at Six Months After Administration of Primaquine With DHA-PQP and DHA-PQP Alone
• Percentage of Participants With Relapse-free Efficacy at Four Months After Administration of Tafenoquine With DHA-PQP and DHA-PQP Alone
• Time to Relapse of P. Vivax Malaria
• Time to Fever Clearance
• Time to Parasite Clearance
• Number of Participants With Recrudescence
• Number of Participants With Any Adverse Events (AEs) and Serious Adverse Events (SAEs) During the Double-blind Treatment Phase

9. Statistical Interpretation

10. Statistical Methods Explained

Several statistical ideas help distinguish the reported results. The primary endpoint is binary: each participant either met the full relapse-free definition or did not. A comparison of the group percentages therefore describes the difference in the probability of meeting that definition at the specified assessment point. The risk difference is the intervention-group proportion minus the comparator-group proportion, expressed in the scale used in the posted recalculation. A value of zero represents equal proportions. Its confidence interval describes a range of values compatible with the data and the calculation method; it is not a guarantee that the true difference lies within that range.

What does the Cox analysis add?

A Cox proportional hazards model is a time-to-event method. In general, it uses information about when events occur, including the ordering and timing of observed events, rather than reducing all follow-up to whether an endpoint was met at one fixed time. A hazard ratio compares instantaneous event rates between groups under the model's proportional-hazards assumption. The registry reports a hazard ratio and confidence interval for the primary comparison, but does not report the event coding, detailed model specification, or checks of the proportional-hazards assumption. A precise interpretation of the direction and clinical meaning of that hazard ratio therefore needs care.

The Cox result and the fixed-time binary comparison can differ because they summarize different aspects of the data. Participants with the same final classification can have events at different times, and the time-to-event method incorporates that timing. The binary endpoint instead reduces follow-up to meeting or not meeting the stated criteria at 6 months. Differences between the methods do not mean that one can be substituted for the other. The registry record identifies both analyses, and their results should be reported with their method and outcome clearly named.

What does the confidence interval describe?

A confidence interval communicates statistical precision around an estimate. For the recalculated risk difference, zero is the value corresponding to no difference in group proportions. The 95% interval runs from -0.046 to 0.246, so it includes zero. For a hazard ratio, the null value is 1, representing equal hazards under the model. The sponsor-reported 95% interval runs from 0.285 to 0.693 and does not include 1. These are intervals for different estimands; comparing their null values does not make the underlying analyses equivalent.

A p-value measures how incompatible the observed data are with a specified null model, assuming the analysis conditions hold. It is not the probability that the null hypothesis is true, nor does it measure the size or practical importance of an effect. The recalculated binary comparison reports p = 0.183, while the sponsor's Cox analysis reports p < 0.001. Since the two p-values arise from different analyses, they answer different statistical questions and should not be read as competing measurements of one identical quantity.

Why are unadjusted recalculations limited?

The risk-difference recalculation uses the posted group counts and simple unadjusted methods. It does not incorporate participant-level follow-up times, covariate adjustment, or other model details that might have been part of the sponsor's analysis. The registry labels a discrepancy, so the sponsor's own analysis takes precedence for the reported trial result. The recalculation remains useful as a transparent check of the posted endpoint percentages, but cannot recreate the sponsor's analysis from aggregate counts alone.

Randomization is intended to support fair comparisons between assigned groups, but a reader also needs to know how allocation was generated, how missing observations were handled, and whether analyses followed prespecified rules. Those details are not reported in the registry record. The primary population is defined, but missing-data methods, sensitivity analyses, and the handling of participants without complete follow-up are not reported. These omissions limit the ability to assess how robust either analysis is to alternative assumptions.

Why does multiplicity matter?

The registry lists multiple secondary outcomes, including efficacy at additional time points, time to relapse, clearance times, recrudescence, and adverse events. When many outcomes or comparisons are examined, the chance of at least one apparently notable result can increase. A prespecified testing hierarchy or adjustment can help manage this issue. The registry record does not report whether multiplicity adjustment was planned or used, so unadjusted secondary p-values should be treated as exploratory rather than as independent confirmation of the primary result.

These points do not invalidate the posted findings. They define what can be concluded from the available summaries: the endpoint percentages, the sponsor's reported time-to-event estimate, and the stated uncertainty can be described, while model details and analysis choices absent from the record remain unresolved.

11. Confidence Intervals and Precision

The primary binary comparison has a risk difference of 0.1, with a 95% confidence interval from -0.046 to 0.246. The interval includes zero, the value representing equal endpoint proportions. Its span indicates that the posted group summaries are compatible with a range of differences, rather than pinning down a narrow estimate. The recalculated p-value is 0.183. These figures describe the simple unadjusted comparison and are not the sponsor's Cox-model result.

The sponsor-reported Cox estimate is a hazard ratio of 0.444, with a 95% confidence interval from 0.285 to 0.693 and p < 0.001. This interval does not include 1, the null value for a hazard ratio. Because the event coding and full model details are not reported in the registry record, the numerical estimate should be interpreted within that limitation. Its interval reflects time-to-event analysis, not the uncertainty around the difference between the two fixed-time percentages.

Confidence intervals are informative about precision, but they do not capture every source of uncertainty. They do not resolve questions about missing data, analysis choices, endpoint measurement, or applicability to populations other than those enrolled. In this trial, the contrast between the binary recalculation and the sponsor's analysis is especially important: their intervals concern different statistical summaries, and the registry flags a discrepancy. The sponsor's own analysis takes precedence as the trial's reported analysis, while the binary interval transparently describes uncertainty in the posted proportions.

Neither an interval excluding its null value nor a small p-value describes the size of a clinically meaningful effect by itself. Conversely, an interval containing the null does not prove that the groups are identical. Precision should be read together with the estimate, the method, the study population, and the incomplete methodological details 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 sample-size figures are planning illustrations based on the observed effect, not the trial's own original design assumptions. For binary outcomes, the figures are participants per arm; for time-to-event calculations, they are total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The original protocol's sample-size justification is not reported in the registry record.

The 80% power column gives the planned number of participants per arm, or total events for a time-to-event calculation, for a hypothetical study with an 80% chance of detecting the specified effect if that effect were the true one and the assumptions held. The 90% power column uses the corresponding 90% target. These are design probabilities under stated assumptions; they do not say what the power of the completed trial was.

Planning for 100% of the observed effect uses the observed estimate as the target effect. Planning for 75% or 50% of the observed effect uses smaller targets. Smaller effects are generally harder to distinguish from random variation, so they require more participants or events to reach the same planned power under the same assumptions. The figures are therefore sensitive to the effect used as the planning target; the observed effect may not be the effect a future study should expect.

These sample-size illustrations are not observed power. They should be read as conditional planning calculations, not as evidence that a completed comparison was adequately or inadequately powered. They also do not replace the trial's unreported original design rationale, and they should not be used to infer why the registry recorded the enrollment it did.

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 = 0.120; treatment proportion p₁ = 0.220; average p̄ = 0.170.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5312 = 1.0412.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5265 = 0.4431.
4. n = (1.0412 + 0.4431)² / (0.1000)² = 220.3, rounded up to 221 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 <- 0.12                          # control proportion
p1 <- 0.22                          # 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(2802501)
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 = 221 (80% power), 295 (90% power)
 75% of observed effect: n per arm = 370 (80% power), 494 (90% power)
 50% of observed effect: n per arm = 778 (80% power), 1,041 (90% power)
power.prop.test: 220.3 
Simulated power at n = 221 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.

14. Analyses Reported by the Sponsor

The sponsor's own analysis of the primary comparison is reported as a Cox proportional hazards analysis. It gives a hazard ratio of 0.444, a 95% confidence interval from 0.285 to 0.693, and p < 0.001; the registry labels the analysis as superiority. The recalculation from the posted six-month endpoint counts instead compares the proportions meeting the binary definition. It gives a risk difference of 0.1, a 95% confidence interval from -0.046 to 0.246, and p = 0.183.

These results differ both in method and in statistical summary. The Cox analysis incorporates time-to-event information, whereas the recalculation uses the group totals meeting a fixed-time endpoint. The registry record does not report enough detail about the Cox model, event coding, or the analysis population for that model to reproduce it from the aggregate endpoint counts. The discrepancy is explicitly flagged in the registry record.

For the trial's reported inference, the sponsor's own analysis takes precedence. The unadjusted recalculation should be understood as a transparent analysis of the posted binary summaries, not as a correction or replacement for the sponsor's model. Both results can be reported accurately when their methods are kept distinct; they should not be combined into a single estimate or treated as if they answered precisely the same question.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary efficacy endpoint and numerous secondary outcomes. These include relapse-free efficacy at additional comparisons or time points, time to relapse, fever and parasite clearance times, recrudescence, and adverse events. Testing many outcomes can increase the chance of obtaining a statistically notable result by chance, especially when several treatment contrasts are considered. Statistical plans often address this by specifying a hierarchy of tests or adjusting significance thresholds, but whether either approach was used is not reported in the registry record.

The record identifies the primary efficacy population as the microbiologic Intent-to-Treat population: randomized participants who received at least one dose of blinded treatment and had microscopically confirmed P. vivax parasitemia at baseline. It does not report the analysis population for every other outcome, nor does it provide a full account of missing observations, withdrawals, incomplete follow-up, or sensitivity analyses. The primary endpoint's definition includes requirements about parasite assessments and concomitant antimalarial medication, but the record does not describe how missing assessments or deviations from those conditions were handled.

The sponsor reports a Cox proportional hazards analysis, but the registry record does not report the complete statistical plan, model specification, event coding, or checks of model assumptions. Interim analyses are not reported in the registry record. The original sample-size justification is also not reported. These absences prevent a full assessment of whether the analysis choices were prespecified and how the sponsor handled potential sources of bias or uncertainty.

These are limits on interpretation, not evidence that a particular procedure was or was not used. The available record supports description of the posted outcomes and the sponsor-reported analysis, but it does not support assumptions about unreported procedures. Multiple secondary results should therefore be treated cautiously, and the discrepancy between the binary recalculation and the sponsor analysis should remain explicit.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: ureterolithiasis (8.3%), cholelithiasis (2.0%), drug-induced liver injury (2.0%), hand fracture (2.0%), electrocardiogram qt prolonged (2.0%).

During the double-blind treatment phase, the registry reports serious adverse events in 1 of 50 participants in the DHA-PQP-only group, 2 of 50 in the tafenoquine plus DHA-PQP group, and 2 of 50 in the primaquine plus DHA-PQP group. Other adverse events were reported in 32 of 50, 36 of 50, and 27 of 50 participants in those respective groups. The registry records no deaths in these groups.

These are counts of participants affected, not a measure of event severity beyond the separate serious-adverse-event classification, and they do not establish that a study drug caused an event. The registry also lists serious-event terms, including ureterolithiasis, cholelithiasis, drug-induced liver injury, hand fracture, electrocardiogram QT prolonged, and hypertensive urgency. The record does not establish from these terms alone which treatment, if any, caused them.

The open-label primaquine phase has separate group records and should not be combined with the double-blind treatment-phase counts. Safety counts are descriptive, and group sizes are limited. The registry record does not provide enough information in these summaries to assess event timing, exposure-adjusted rates, or causal attribution.

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

The posted data show that a larger observed proportion of participants in the tafenoquine plus DHA-PQP group met the six-month relapse-free efficacy definition than in the DHA-PQP-only group. The simple unadjusted comparison has a confidence interval that includes zero, while the sponsor's Cox analysis reports a hazard ratio with a confidence interval that does not include 1 and a p-value of <0.001. Because the two analyses summarize different features of follow-up, they should be interpreted separately. The registry flags the discrepancy, and the sponsor's own analysis takes precedence as the reported trial analysis.

The result does not establish that the treatment will have the same effect in other populations or settings. The trial enrolled male Indonesian soldiers with P. vivax malaria, and people with G6PD deficiency were excluded. The record describes a single-center study and a 6-month primary follow-up. Those features define the evidence available and limit direct generalization beyond the enrolled group and study conditions.

The result also does not show that a treatment caused or prevented every recurrence, nor does the endpoint percentage describe the timing of events. The endpoint applies a specific composite set of criteria involving baseline infection, initial clearance, subsequent parasite assessments, other antimalarial medication, and parasite-free status at 6 months. The sponsor's time-to-event analysis supplies a different summary, but key model details are not reported.

The safety summaries describe reported adverse events and serious adverse events in the recorded groups; they do not by themselves establish causation or compare risk with precision. Missing-data methods, multiplicity procedures, the full statistical plan, and other analytic details are not reported in the registry record. The appropriate conclusion is therefore bounded: describe the posted proportions and the sponsor-reported analysis, retain their methodological distinction, and avoid extending either result beyond the evidence recorded.

18. Why This Trial Matters Statistically

This trial illustrates why clinical trial results need to be read through the lens of their estimands. A fixed-time binary outcome asks what proportion met a defined criterion by a particular assessment point. A time-to-event model uses when events occurred. Both can be relevant to the same clinical question, but they are not identical summaries and can yield different estimates and inferential conclusions. Keeping the method attached to each estimate prevents a hazard ratio from being mistaken for a risk difference or vice versa.

The example also shows why confidence intervals matter. The recalculated risk difference has an interval that includes its null value, while the sponsor-reported hazard-ratio interval excludes its null value. A point estimate or p-value alone would conceal that the analyses differ in outcome representation, assumptions, and available detail. Clear reporting of the model, event coding, population, and missing-data approach would help readers understand why analyses differ and how sensitive conclusions may be to analytic choices.

Multiple secondary outcomes create a further statistical challenge. Without a reported multiplicity strategy, secondary findings can provide useful context but should not be treated as a set of independent confirmatory tests. Similarly, planning calculations based on an observed effect illustrate how assumptions affect sample-size needs; they do not reveal the trial's original design rationale or the completed study's observed power.

For clinical researchers and biostatisticians, the central lesson is to report the population, endpoint definition, analysis method, estimate, and uncertainty together. This trial's registry record permits a careful account of those elements where available, while also making visible the limits imposed by incomplete methodological detail and the discrepancy between the posted binary summaries and the sponsor analysis.

19. Limitations

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

The enrolled population was specific: male Indonesian soldiers diagnosed with P. vivax malaria after return from deployment to a malarious region. The trial was conducted at a single center, and people with G6PD deficiency were excluded. These eligibility and setting features restrict how directly the results can be extended to other populations. The primary outcome was assessed at 6 months, so the posted primary result does not describe outcomes beyond that follow-up.

The primary group summaries contain 50 participants per arm. The binary endpoint estimate is therefore accompanied by a confidence interval spanning values on both sides of zero. The sponsor's time-to-event analysis has a different result, but the registry record does not report the event coding, complete model specification, or assumption checks needed to independently interpret and reproduce it. The flagged discrepancy between the sponsor's analysis and the simple recalculation cannot be reconciled from the posted aggregate summaries.

The registry record does not report the original sample-size justification, full statistical analysis plan, missing-data approach, interim analyses, or multiplicity procedures. It also does not supply enough information to assess how missing or incomplete follow-up may have affected the endpoint summaries. These omissions constrain evaluation of prespecification, robustness, and the weight of secondary findings.

The registry describes the primaquine group as an informal comparison, which limits how that group should be used to interpret the primary question. Safety information is presented as counts of affected participants; the summarized counts do not establish causation or provide exposure-adjusted comparisons. These limitations call for cautious interpretation of the registry results without implying that unreported methods were absent or that particular biases necessarily occurred.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety Study of Tafenoquine (TQ) Co-administered With Dihydroartemisinin-piperaquine (DHA-PQP) for the Radical Cure of Plasmodium Vivax (P. Vivax) Malaria — NCT02802501.
• Registry record last updated 2020-07-24; status last verified 2020-06.
• Results first posted 2020-07-24.
• 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

NCT02802501 was a completed Phase 3, randomized, parallel-group, placebo-controlled superiority study of tafenoquine co-administered with DHA-PQP for P. vivax malaria. The primary comparison was tafenoquine plus DHA-PQP versus DHA-PQP alone, with primaquine plus DHA-PQP included as an informal comparator. The recorded enrollment was 150, with 50 participants in each treatment group in the posted efficacy comparisons.

The primary outcome was the percentage meeting the study's relapse-free efficacy definition at 6 months post-dose in the microbiologic Intent-to-Treat population. The binary endpoint summaries and the sponsor's Cox proportional hazards analysis differ in their method and statistical conclusion; the registry flags a discrepancy, and the sponsor's own analysis takes precedence as the reported trial analysis.

The registry also posts secondary efficacy and safety outcomes. The original sample-size justification, full analysis plan, multiplicity procedures, and missing-data methods are not reported in the registry record. Those omissions, alongside the trial's specific population and setting, should be considered when interpreting the reported findings.