Long-Term Safety Study of Tafenoquine: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Long-Term Safety Study of Tafenoquine (NCT03320174), a randomized phase 2 study. The primary outcome is Serious Ophthalmic Safety Event.

2. Clinical Question

3. Trial Design

This was a Phase 2, randomized, parallel-group study described as single site, double blind, and placebo controlled. The registry identifies quadruple masking. Enrollment was recorded as 600, and the trial status is completed. The study began on 2017-10-05, with primary completion on 2021-07-13.

Participants were assigned to tafenoquine 200 mg or placebo. Both regimens began with daily dosing for three consecutive days and continued with once-weekly dosing for 51 weeks. The brief summary describes safety follow-up visits at Weeks 4, 12, 24, and 52, an end-of-study visit at Week 64, and additional assessment for an ongoing adverse event at Week 64. The registry record does not report the trial’s original sample-size justification or the assumptions used to plan enrollment.

The primary ophthalmic endpoint is reported in a per-protocol population. Participants qualified for this population if they received at least 25% of the total planned investigational product dose, had at least one valid baseline and post-baseline evaluation by SD-OCT and qFAF, and had no major protocol deviations. The posted primary endpoint counts are based on 247 participants in the tafenoquine group and 253 in the placebo group. These analysis counts should not be treated as a restatement of the enrollment figure: they refer to the endpoint’s stated analysis population.

The study also listed visual acuity, corneal examination, retinal photography, microperimetry, and color-vision outcomes. There were 12 outcome measures and 10 analyses recorded overall, with 11 secondary outcomes posted. The registry record does not report further detail on the study’s original statistical plan or the handling of interim analyses.

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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: All subjects who received at least 25% of the total planned dose for IMP, had at least one valid baseline and post baseline evaluation by SD-OCT and qFAF, and had no major protocol deviations were included in the Per-Protocol population.

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 Serious Ophthalmic Safety Event, measured over After 12 months of exposure to study drug.

The primary endpoint was the number of participants with one or more protocol-defined serious ophthalmic safety events after 12 months of exposure to study drug. The registry describes these events as significant retinal changes from baseline assessed using SD-OCT and qFAF. The endpoint is a participant count: each qualifying participant contributes to the event count, rather than the endpoint measuring the size of an individual retinal change.

A binary participant-level endpoint is useful for comparing how often a defined event was observed in each randomized group. It can make the comparison clinically interpretable as a difference in event occurrence, but it does not show the timing, duration, or detailed character of events unless those are separately reported. The registry record does not provide the full protocol definition or thresholds for a serious ophthalmic safety event beyond the description of significant retinal changes from baseline using SD-OCT and qFAF.

The endpoint is restricted to a per-protocol population with specified dose exposure, valid baseline and follow-up imaging, and no major protocol deviations. This restriction matters when interpreting the counts: they characterize participants meeting those conditions, not necessarily all enrolled participants. The observed event counts were 45 with tafenoquine and 48 with placebo. The comparison estimates the relative group difference in this defined endpoint; it does not establish that all possible ophthalmic or other safety outcomes were alike.

7. Results Posted in the Registry

• Tafenoquine 200 mg (2 x 100 mg Tablets): 18.2% (45/247) versus 19.0% (48/253) on control; risk difference -0.8 percentage points (95% CI -7.6 to 6.1), risk ratio 0.96 (0.67–1.39); unadjusted two-proportion z-test p = 0.829.

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 Participants With Mean Change From Baseline in Best Corrected Visual Acuity

• 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:
  • Tafenoquine 200 mg (2 x 100 mg Tablets): 0.0% (0/247) versus 0.8% (2/253) on control; risk difference -0.8 percentage points (95% CI -1.9 to 0.3); unadjusted two-proportion z-test p = 0.161.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tafenoquine 200 mg (2 x 100 mg Tablets) and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Corneal Deposits From Slit Lamp Examination of the Corneal Epithelium

• 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:
  • Tafenoquine 200 mg (2 x 100 mg Tablets): 71.3% (176/247) versus 18.6% (47/253) on control; risk difference 52.7 percentage points (95% CI 45.3 to 60.1), risk ratio 3.84 (2.93–5.02); 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 Tafenoquine 200 mg (2 x 100 mg Tablets) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants With New Abnormalities Compared With Baseline Observed With Color Retinal Digital Photography

• 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:
  • Tafenoquine 200 mg (2 x 100 mg Tablets): 46.2% (114/247) versus 6.3% (16/253) on control; risk difference 39.8 percentage points (95% CI 32.9 to 46.7), risk ratio 7.30 (4.46–11.95); 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 Tafenoquine 200 mg (2 x 100 mg Tablets) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover several aspects of ophthalmic assessment, including visual acuity, corneal findings, retinal imaging, microperimetry, and color vision. Across the detailed comparisons, the observed pattern is not uniform: some structural or imaging findings were more frequent in the tafenoquine group, while the best-corrected visual-acuity outcome involved few participants. This broader pattern adds context to the primary endpoint, but it does not replace or redefine the primary comparison.

The primary endpoint focused on protocol-defined serious ophthalmic safety events assessed through SD-OCT and qFAF. Secondary outcomes measured other features, used their own definitions, and may capture findings of different severity or clinical meaning. A result on one secondary measure therefore cannot be treated as confirmation of the primary endpoint, nor does a difference in a secondary measure automatically establish a serious ophthalmic safety event.

The posted secondary comparisons are unadjusted. When multiple outcomes are examined, the chance of at least one apparently notable result increases. In general, multiplicity procedures or a prespecified hierarchy can help control how a family of tests is interpreted, but the registry record does not report such a strategy. The secondary findings should therefore be considered exploratory and interpreted in the context of their definitions, uncertainty, and the overall study design, rather than as separate definitive tests.

Although 11 secondary outcomes are recorded as posted, detailed comparative results are not reported in the registry record for every listed outcome in the available results. Conclusions should be limited to the outcomes with posted comparative data. The secondary pattern may motivate careful attention to ophthalmic findings in interpreting this trial, but it cannot settle questions about unreported outcomes or establish a causal explanation for observed differences.

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

• Number of Participants With Mean Change From Baseline in Key SD OCT Parameters
• Number of Participants With Ellipsoid or Interdigitating Zone Disruption
• Number of Participants With Mean Change From Baseline in Best Corrected Visual Acuity
• Number of Participants With Corneal Deposits From Slit Lamp Examination of the Corneal Epithelium
• Number of Participants With New Abnormalities Compared With Baseline Observed With Color Retinal Digital Photography
• Number of Participants With New Abnormalities Compared With Baseline Observed With Microperimetry
• Number of Participants With Any Clinically Significant Change in ETDRS BCVA (Defined as >15 Letter Change [≥ 3 Lines] of Change in ETDRS BCVA at 4 Meters)
• Proportion of Participants Who Develop a Color Deficiency Using the Farnsworth-Munsell 100 (FM-100) Hue Test

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary result is a comparison of a binary outcome: whether each participant had one or more serious ophthalmic safety events. The group summaries give the number of participants with the event and the number included in each group. A risk is the proportion of participants in a group who experienced the event. A risk difference expresses the contrast between those group risks. A value near zero indicates little estimated difference in event frequency, while a value on either side of zero indicates the direction of the estimated difference.

What does a confidence interval describe?

In general, a confidence interval represents uncertainty around an estimate under a specified statistical model and repeated-sampling framework. It is not a range containing a known true effect with certainty, and it does not assign a probability to a particular effect after the data have been observed. For this primary comparison, the recalculated confidence interval includes zero, the value corresponding to no risk difference. That means the data do not rule out no difference at the confidence level used for the reported interval. The interval also permits effects in either direction, so the estimate should not be treated as precise evidence that the groups are equivalent.

How should the p-value be read?

In general, a p-value measures how unusual data at least as incompatible with a null hypothesis would be if that null hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, the probability that the result occurred by chance, or a measure of clinical importance. The recalculated unadjusted p-value for the primary comparison is 0.829. Considered with the confidence interval, this does not provide evidence against a no-difference null hypothesis. It does not prove no effect.

Why use the risk difference?

For a binary outcome, the risk difference gives an absolute contrast between group event frequencies. It is one way to describe how much the observed event frequency differs between assigned groups. Other effect measures, such as a risk ratio or odds ratio, express relative rather than absolute contrasts. The choice of scale affects how a comparison is communicated; no single scale captures every aspect of the data. The primary reported analysis uses a risk difference, and the recalculation also uses that scale. The registry record does not report an adjusted primary estimate.

Randomization supports a comparison between assigned groups, while masking is intended to limit the influence of knowledge of assignment on trial conduct and assessment. These design features do not remove uncertainty from the observed data or address missing outcome information automatically. The primary analysis population is per protocol, with eligibility based on dose received, imaging availability, and protocol deviations. The registry record does not report how missing endpoint values were handled, whether any sensitivity analyses were done, or whether the primary analysis adjusted for other variables.

What does equivalence require?

In general, an equivalence analysis asks whether the data are sufficiently precise to rule out differences larger than a prespecified acceptable margin in either direction. A result that is not statistically significant in a conventional test of no difference does not, on its own, demonstrate equivalence. Interpretation depends on the margin, confidence interval, and prespecified analysis method. The sponsor’s reported analysis is labelled equivalence, but the registry record does not report the equivalence margin or enough detail to independently assess that conclusion. The sponsor’s reported analysis should be distinguished from the unadjusted recalculation.

The primary endpoint is a count of participants with an event, not a count of all event episodes. If a participant had more than one qualifying finding, the endpoint description indicates that the participant is counted as having one or more events; the posted endpoint is therefore not an episode-rate analysis. The registry record does not provide additional detail on event adjudication or the handling of repeated findings.

For secondary binary endpoints, the posted recalculations use the same general comparison logic: group event proportions are contrasted using a risk difference, with a confidence interval and an unadjusted p-value where reported. These comparisons are unadjusted in the sense that no multiplicity correction is included in the posted p-values. In general, testing many outcomes increases the chance that at least one result appears notable even when there is no underlying effect. This makes the broader pattern and prespecified hierarchy important, but the registry record does not report a multiplicity strategy.

The sample-size illustrations use a normal approximation, two-sided significance level 0.05, equal allocation, and effects defined as stated fractions of the observed effect. Those are assumptions for the posted planning illustration, not documented assumptions for the original trial design. The original design assumptions and sample-size justification are not reported in the registry record.

11. Confidence Intervals and Precision

The primary estimate is close to no difference, but the confidence interval is the more informative guide to precision. The recalculated interval extends across zero, so the observed data are compatible with a lower or higher event frequency in the tafenoquine group. Its breadth means that a near-zero point estimate alone should not be read as evidence that the groups have the same underlying risk.

The sponsor’s reported 95% confidence interval runs from -7.6 to 6.1 for the reported risk difference. It also spans zero. The registry record does not state the units or the equivalence margin for this reported analysis, so those values cannot be used to judge whether the interval lies entirely within a prespecified equivalence range. The label “equivalence” records the sponsor’s analysis classification, but the margin and supporting analysis details are not reported in the registry record.

Precision is affected by the number of observed events as well as the number of participants, and binary outcomes with relatively few events can leave substantial uncertainty even when the group counts are similar. In general, more precise estimates have narrower intervals, while less precise estimates have wider intervals. The endpoint population and eligibility rules also matter: the interval pertains to the stated per-protocol analysis, not automatically to all enrolled participants.

The confidence interval does not address biases from missing outcome data, deviations from the analysis population, or selective reporting. Those issues require details about analysis methods and data handling, which are not reported in the registry record. The primary result is best described as an imprecise estimate that does not identify a clear difference, rather than as proof of no difference.

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 expressed as participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The posted calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a stated fraction of the observed effect as the effect to detect. The trial’s original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column means the illustrated design would have an 80% chance of detecting the specified effect at the stated significance level if the assumptions used for the calculation held. The 90% column represents a higher chance of detecting that effect under those assumptions, and therefore generally requires more participants per arm. These statements describe hypothetical future planning, not what happened in the completed trial.

The rows scale the observed effect to 100%, 75%, and 50%. A smaller effect is harder to distinguish from random variation, so smaller effects require more participants. This is especially important when the observed effect is used as the starting point: planning around a smaller fraction is a way to illustrate the consequence of targeting a more modest difference, not evidence that such an effect will occur.

These figures are not observed power. They do not measure the probability that the completed study’s result is correct, and they do not alter the uncertainty in the observed estimate. Planning values based on an observed effect can be unstable, particularly when the estimate is uncertain. The primary comparison’s confidence interval remains the relevant description of precision for the posted result.

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 = 0.190; treatment proportion p₁ = 0.182; average p̄ = 0.186.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5502 = 1.0784.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5502 = 0.4631.
4. n = (1.0784 + 0.4631)² / (-0.0075)² = 41,828.7, rounded up to 41,829 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 <- 0.189723320158103                          # control proportion
p1 <- 0.182186234817814                          # 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(3320174)
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 = 41,829 (80% power), 55,997 (90% power)
 75% of observed effect: n per arm = 74,654 (80% power), 99,940 (90% power)
 50% of observed effect: n per arm = 168,623 (80% power), 225,738 (90% power)
power.prop.test: 41828.7 
Simulated power at n = 41,829 per arm: 0.801 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s reported analysis labels the primary comparison as equivalence and gives a risk difference of -0.754 with a 95% confidence interval from -7.6 to 6.1. The reported analysis does not include a p-value in the registry record. The unadjusted recalculation based on the posted group summaries estimates a difference close to zero, has a confidence interval that crosses zero, and gives an unadjusted p-value of 0.829. These results are directionally consistent in that neither identifies a clear difference, but they are different presentations and should not be conflated.

The sponsor’s reported values are the trial’s own analysis. The registry record does not state the units for its risk-difference figures, the equivalence margin, or sufficient analysis details to verify how the equivalence designation was reached. Without the margin and protocol-level methods, the label cannot be independently evaluated from the registry record alone. A conventional non-significant result in an unadjusted recalculation is not a substitute for the sponsor’s equivalence analysis.

The registry record does not indicate a discrepancy between the reported and recalculated results. The recalculation is a simple, unadjusted check from the posted summaries and does not replace the sponsor’s analysis or account for any methods not captured in those summaries. The sponsor’s analysis should be read as the reported trial analysis, while the recalculation offers a transparent view of the summary counts and their uncertainty.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint and multiple secondary outcomes, including several ophthalmic measurements. Testing more than one outcome creates a multiplicity concern: even when no true group differences exist, a collection of tests is more likely to produce at least one result that appears statistically notable. In general, prespecified outcome hierarchies, family-wise error procedures, or other multiplicity strategies can guide interpretation. The registry record does not report whether any such strategy was planned or applied.

The secondary comparisons include unadjusted p-values. They should not be treated as though each were the sole confirmatory test. The record does not report a prespecified multiplicity procedure, a hierarchy for the secondary outcomes, or a strategy for interpreting results across the full outcome set. This limits the strength of conclusions drawn from isolated secondary findings.

The primary endpoint population is defined by dose exposure, availability of valid baseline and post-baseline SD-OCT and qFAF assessments, and absence of major protocol deviations. This is a per-protocol population. The adverse-event summary uses different at-risk counts, and the record does not provide enough detail to treat those safety summaries as the same analysis population. Results from these different populations should be interpreted separately.

The registry record does not report how missing primary or secondary outcome data were handled, whether participants with incomplete evaluations were included in sensitivity analyses, or how the analysis addressed deviations beyond the stated per-protocol criteria. It also does not report imputation methods or a missing-data assumption. Consequently, the impact of missing observations on the estimated comparisons cannot be assessed from the registry record.

The original statistical analysis plan, interim-analysis procedures, and sample-size justification are not reported in the registry record. Their absence limits assessment of whether outcome definitions, analysis populations, and multiplicity decisions were established before results were available. These gaps do not invalidate the posted summaries, but they restrict how fully their confirmatory status and robustness can be evaluated.

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: meniscus injury (1.0%), pancreatitis acute (0.7%), periorbital cellulitis (0.7%), suicide attempt (0.7%), anorectal disorder (0.3%).

The adverse-event summary reports serious adverse events among 23 participants at risk in the tafenoquine group and 17 at risk in the placebo group. The corresponding at-risk counts were 301 and 299. The record reports no deaths in either group. These are participant counts from the adverse-event summary and should not be confused with the primary ophthalmic endpoint counts, which use a per-protocol population and different group sizes.

The listed serious-event terms include meniscus injury, acute pancreatitis, periorbital cellulitis, suicide attempt, anorectal disorder, and inguinal hernia, with the posted percentages ranging from 0.3% to 1.0%. The terms are descriptive safety listings; the registry record does not establish that each event was caused by study treatment. Counts alone do not describe event timing, severity beyond the serious classification, or the clinical course.

The non-serious adverse-event summary is recorded separately. The registry record does not provide a basis for combining serious and non-serious event counts or for inferring comparative causality from these summary figures. Safety findings should be read as reported events in the stated at-risk groups, not as a complete assessment of every possible risk.

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

The primary result describes the observed frequency of a defined serious ophthalmic endpoint in the per-protocol population after 12 months of exposure. The observed counts were similar in the two groups, and the unadjusted recalculation does not identify a clear difference. Its confidence interval crosses no difference, leaving uncertainty about the direction and size of any underlying contrast.

This result does not prove that tafenoquine and placebo have identical ophthalmic safety profiles. A failure to identify a difference is not proof of equivalence, and an equivalence claim requires a prespecified margin and an analysis showing that the interval is sufficiently narrow relative to that margin. The sponsor labels its reported analysis as equivalence, but the registry record does not report the margin or enough detail to independently assess the equivalence conclusion.

The endpoint is specifically defined around significant retinal changes from baseline assessed with SD-OCT and qFAF. It does not cover every possible ocular outcome, all adverse events, or long-term effects beyond the recorded assessment context. Separate secondary outcomes and adverse-event listings provide additional observations but have different definitions and analysis populations.

The findings also apply to the study’s selected population and regimen: healthy, G6PD-normal volunteers in a randomized placebo-controlled study, with the primary estimate based on the specified per-protocol criteria. They should not be generalized beyond those conditions without further evidence. The posted data describe what was recorded in this trial; they do not provide individual medical guidance or establish a treatment recommendation.

Finally, uncertainty from the confidence interval is distinct from uncertainty arising from missing data, multiplicity, or choices in analysis. Because details about missing-data handling, multiplicity, and the original statistical plan are not reported in the registry record, those issues cannot be fully assessed from the posted summaries.

18. Why This Trial Matters Statistically

This study illustrates why a small difference between observed event counts should not be interpreted without an uncertainty estimate. The primary point estimate is close to no difference, but the confidence interval includes both directions of effect. The appropriate statistical reading is therefore not simply that the groups look similar; it is that the available estimate does not clearly distinguish a difference and is not precise enough, on its own, to establish equivalence.

It also highlights the distinction between a trial’s sponsor-reported analysis and a simple recalculation from group summaries. The sponsor labels its result as equivalence, while the registry record does not include the margin needed to assess that designation independently. An unadjusted recalculation can help readers understand the observed counts, but it cannot replace the trial analysis or recover missing protocol-level details.

Several ophthalmic secondary outcomes broaden the safety picture beyond the primary endpoint. Their varied pattern shows why endpoint definitions matter: imaging findings, visual acuity, and serious protocol-defined events are not interchangeable. Since multiple secondary comparisons were made and no multiplicity strategy is reported, isolated secondary results require caution.

Finally, the primary analysis population and the adverse-event population differ. Keeping the populations distinct, and recognizing what is not reported about missing data and the original analysis plan, is essential to a sound statistical reading. These are general lessons in interpreting clinical trial registries as well as considerations specific to this study.

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.

The primary result is based on a per-protocol population rather than all enrolled participants. Eligibility required a minimum level of planned dose exposure, valid baseline and follow-up imaging, and no major protocol deviations. This may limit how directly the endpoint estimate applies to every participant assigned in the trial. The registry record does not report the consequences of excluding participants who did not meet those criteria.

The registry record does not report the equivalence margin, the full statistical analysis plan, the original sample-size justification, or interim-analysis procedures. Without these details, the sponsor’s equivalence designation cannot be independently evaluated, and it is not possible to determine from the registry record whether all analysis choices were prespecified.

Missing-data methods are not reported. The effect of incomplete ophthalmic assessments on the primary and secondary results therefore cannot be assessed. The registry record also does not report a multiplicity strategy for the numerous ophthalmic outcomes, so secondary comparisons require cautious interpretation.

The detailed secondary results are not reported for every listed outcome, despite 11 secondary outcomes being recorded as posted. The available comparative findings cannot resolve questions about outcomes without detailed results. The adverse-event summary uses at-risk counts that differ from the primary endpoint population, and the event counts do not establish causality.

Finally, the study was conducted in healthy G6PD-normal volunteers and evaluates a specific dosing schedule and assessment period. The registry record does not establish whether its results generalize to other populations, regimens, or longer-term contexts. These limitations qualify interpretation; they do not erase the information contained in the reported results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Long-Term Safety Study of Tafenoquine — NCT03320174.
• Registry record last updated 2026-04-17; status last verified 2025-09.
• Results first posted 2026-04-17.
• 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

NCT03320174 is a completed Phase 2 randomized, parallel, placebo-controlled study of tafenoquine, described as single site and quadruple masked. It enrolled healthy volunteers and compared a tafenoquine regimen with placebo following daily dosing for three consecutive days and weekly dosing for 51 weeks.

The primary endpoint was the count of participants with one or more protocol-defined serious ophthalmic safety events after 12 months of exposure, assessed using SD-OCT and qFAF. The per-protocol counts were 45 in the tafenoquine group and 48 in the placebo group. The unadjusted comparison does not identify a clear difference, and its confidence interval includes no difference. The sponsor’s reported analysis is labelled equivalence, but the registry record does not report the equivalence margin.

Secondary ophthalmic findings and adverse-event summaries add context, but multiplicity handling and missing-data methods are not reported. The results should be interpreted within the stated analysis populations and the limits of the registry record.