Artemisinin-Based Combination Therapy: Clinical Trials in Cameroon: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Artemisinin-Based Combination Therapy: Clinical Trials in Cameroon (NCT00297882), a randomized phase 3 study. The primary outcome is Cure Rate on Day 28.

2. Clinical Question

3. Trial Design

This was a randomized, single-masked, parallel-group Phase III trial of artemether-lumefantrine (AL) and amodiaquine-artesunate (AQ-AS) for malaria in children in Cameroon. The registry lists enrollment of 816. The posted Day 28 outcome has 204 participants in the AL group and 612 in the AQ-AS group. The treatment descriptions specify a 3-day course for both combinations, with different dosing schedules and drug combinations.

The record lists a start date of 2006-07, primary completion in 2009-04, and a completed status. It describes three study centres, but the locations are not consistent across the record: the brief summary names Banso, Limbe, and Garoua, while the primary outcome description names Mutengene, Bangolan, and Garoua. How these place names relate to one another is not reported in the registry record.

The primary outcome was Cure Rate on Day 28, measured from Day 0 - 28. Cure Rate Day 14 was posted as a secondary outcome. The brief summary says efficacy was assessed using a WHO standardized 28-day protocol and that safety was monitored through clinical examination and biochemical and hematological indices. It also describes investigation of molecular markers and gametocyte carriage. The registry record does not report the detailed analysis populations, how participants with missing outcome assessments were handled, or the protocol-specific criteria used to classify a cure.

Randomization and a parallel-group comparison allow the outcomes to be compared between the assigned treatment groups, subject to the trial’s allocation procedures and follow-up. The allocation sequence, concealment procedures, and masking details are not reported in the registry record. Single masking is listed, but the masked party or parties are not identified.

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.

Day 14

Reasons for not completing this period:

Day 28

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Children aged 6 months-10 years in different locations in Cameroon.

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 Cure Rate on Day 28, measured over Day 0 - 28.

The primary endpoint is the number of participants classified as cured on Day 28. The posted results report 197 of 204 participants in the AL group and 603 of 612 in the AQ-AS group as having a cure outcome. The endpoint is binary at the participant level: each participant is classified according to whether the specified cure outcome occurred. The registry lists the outcome unit as participants and the measurement timeframe as Day 0 - 28.

A fixed-time cure outcome is used to assess antimalarial efficacy over the stated follow-up period. The brief summary says that drug efficacy was determined using a WHO standardized 28-day protocol. Such a protocol provides a defined period for assessing outcomes after treatment; the particular criteria and any adjustments used in this trial are not reported in the registry record.

The endpoint is not a measure of every dimension of treatment response. In particular, the primary result alone does not describe safety, the timing of any recurrence, parasite resistance markers, or gametocyte carriage. The registry lists these as areas of interest in the study summary, but the posted primary result concerns cure status at Day 28.

7. Results Posted in the Registry

• 2 Amodiaquine-Artesunate AQ-AS: 98.5% (603/612) versus 96.6% (197/204) on control; risk difference 2.0 percentage points (95% CI -0.7 to 4.6), risk ratio 1.02 (0.99–1.05); unadjusted two-proportion z-test p = 0.080.

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.

Cure Rate Day 14

• 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:
  • 2 Amodiaquine-Artesunate: 92.0% (563/612) versus 94.1% (192/204) on control; risk difference -2.1 percentage points (95% CI -6.0 to 1.8), risk ratio 0.98 (0.94–1.02); unadjusted two-proportion z-test p = 0.318.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 2 Amodiaquine-Artesunate and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome is Cure Rate Day 14. Its recalculated unadjusted comparison points in the opposite direction from the Day 28 primary estimate, while its confidence interval spans zero. This gives no clear statistical separation between the groups at that assessment. The overall pattern is therefore not a consistent indication of a difference favoring the same group across the posted follow-up assessments.

The primary endpoint remains the main basis for interpreting the trial’s stated efficacy question. A secondary assessment can add context about the pattern over time, but it does not replace the primary endpoint or resolve uncertainty in the primary comparison. The Day 14 and Day 28 results also concern distinct assessment times, so they should not be merged into a single effect estimate without a prespecified method.

In general, examining multiple outcomes or time points increases the opportunity to observe an apparently notable result by chance. An unadjusted secondary p-value does not account for that multiplicity. The registry record does not report a multiplicity adjustment or a hierarchy governing interpretation of secondary outcomes. Consequently, the secondary result should carry less evidential weight than a primary result defined in advance, and it should be interpreted as supporting context rather than a standalone confirmatory finding.

The registry lists Cure Rate Day 14 as the posted secondary outcome. The brief summary also describes safety monitoring, molecular sequencing, parasite profiles, and gametocyte carriage as study aims, but those descriptions do not establish that corresponding outcome results are posted as secondary efficacy analyses. Results for any further outcomes are not reported in the registry record.

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

• Cure Rate Day 14

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a binary outcome: participants with a cure event. The comparison can therefore be expressed using group proportions, risk differences, risk ratios, or odds ratios. The posted recalculation focuses on the unadjusted risk difference, which contrasts the proportion classified as cured in the AQ-AS group with the corresponding proportion in the AL group. A positive risk difference means the observed proportion is higher in AQ-AS; a negative difference means it is lower. The recalculated result is unadjusted, meaning it is based on the posted group summaries rather than an adjustment for other variables.

What does the risk-difference interval tell the reader?

A confidence interval describes a range of values compatible with the data and the statistical method, under the method’s assumptions. It conveys uncertainty around the estimated risk difference; it is not a range containing a specified proportion of individual participants’ outcomes. For the Day 28 comparison, the recalculated interval spans zero. Zero represents no risk difference, so the interval does not rule out no difference. It also includes values on either side of zero, representing possible differences favoring either group. The registry’s sponsor analysis reports a 95% confidence level, but its numerical interval is not reported in the registry record.

The recalculated comparison also includes risk-ratio and odds-ratio estimates. A risk ratio compares the proportions with the event, while an odds ratio compares the odds of the event. For both measures, the null value is one, representing no relative difference. The posted intervals for these measures include their null value. These measures offer different scales for expressing the same binary outcome and should not be mistaken for adjusted effects or for evidence that one group is clinically superior.

How should the p-values be read?

The unadjusted p-value assesses how compatible the observed data are with a null hypothesis of no group difference under the chosen statistical model. It does not give the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The Day 28 recalculation gives p = 0.08; the Day 14 recalculation gives p = 0.318. Neither value, on its own, proves equivalence or non-inferiority. In general, the estimate and confidence interval are needed alongside a p-value to understand both the direction and precision of a comparison.

The sponsor’s posted analysis is described as a two-sided t-test, with a 95% confidence level and a result of p > 0.05. The registry does not identify the exact quantity tested by that t-test, show a numerical estimate or confidence limits for it, or give details of the non-inferiority framework. As a result, the sponsor’s test cannot be fully reconstructed from the registry record. The recalculated tests are simple, unadjusted comparisons based on the posted summaries; they are not a replacement for a prespecified analysis that may use additional trial information.

Why do trial details matter to the statistical interpretation?

Randomization is intended to make the treatment groups comparable in expectation, reducing systematic differences in baseline characteristics. The record identifies the trial as randomized but does not report sequence generation or allocation concealment. Single masking is reported, but who was masked is not. These omissions limit assessment of possible biases affecting treatment assignment, outcome assessment, or participant behavior.

Outcome classification also matters. The record says the cure assessment used a WHO standardized 28-day protocol, but it does not report the operational cure criteria or how recurrent infection was treated in the primary analysis. The summary mentions molecular assessment of recrudescence or reinfection, but it does not explain how those assessments fed into the posted cure counts. The registry record also does not report whether the primary comparison followed intention-to-treat, per-protocol, or another analysis population.

For binary outcomes, counts and denominators describe the observed results, while inferential methods quantify uncertainty under assumptions about the data and analysis. In general, missing outcome data can affect both the estimated event proportions and the validity of the comparison if missingness differs between groups or is related to outcome. The handling and extent of missing primary outcomes are not reported in the registry record. The posted denominators therefore should not be taken as proof that every randomized participant had a complete assessment.

Finally, because the primary result is framed as non-inferiority, interpretation requires more than a conventional test for any difference. In general, a non-inferiority analysis asks whether the data rule out a loss larger than a prespecified acceptable margin. The margin, its justification, and the relevant analysis population are not reported in the registry record. A result of p > 0.05 from a two-sided test of difference is not, by itself, a demonstration of non-inferiority.

11. Confidence Intervals and Precision

The Day 28 recalculated confidence interval for the risk difference spans zero. This means the posted data do not precisely distinguish a positive difference from no difference or a difference in the opposite direction. The interval’s width reflects uncertainty in the estimated contrast; the observed counts alone should not be read as a precise estimate of the underlying treatment difference.

The interval is also relevant to the non-inferiority label. In general, a non-inferiority assessment compares the confidence interval with a prespecified margin, rather than relying only on whether a test for any difference crosses a conventional significance threshold. The margin and the sponsor’s numerical confidence limits are not reported in the registry record. The registry lists a 95% confidence level for the sponsor’s analysis, but the interval itself is not posted there.

The Day 14 recalculated interval also spans zero, and its unadjusted p-value is 0.318. The primary and secondary estimates therefore both have uncertainty that includes no difference, though they point in different directions. That pattern makes it important to avoid overstating small differences suggested by the point estimates. It does not establish that the underlying effects are exactly equal.

Confidence intervals address statistical uncertainty under a specified method; they do not account for every limitation. In particular, an interval does not resolve uncertainty arising from unreported endpoint definitions, missing-data procedures, analysis populations, or the inconsistent descriptions of study locations. The posted confidence intervals are unadjusted recalculations from summary statistics, so they may not reflect adjustments or analyses used by the sponsor.

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, not total participants or total events. They are illustrations based on the observed effect, using a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting a stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

For the Day 28 outcome, planning for 100% of the observed effect gives 976 participants per arm for 80% power and 1,305 participants per arm for 90% power. Planning for 75% of the observed effect gives 1,904 participants per arm for 80% power and 2,548 participants per arm for 90% power. Planning for 50% of the observed effect gives 4,662 participants per arm for 80% power and 6,240 participants per arm for 90% power.

The 80% power column represents the illustrative number per arm under which the assumed effect would be detected in 80% of repeated trials if the planning assumptions and model were correct. The 90% column uses a higher target probability of detection, so it requires more participants under the same assumptions. Smaller effects are harder to distinguish from random variation and therefore require more participants. The corresponding Day 14 planning figures use the same stated assumptions and are also per arm. These are planning illustrations, not observed power.

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 = 0.966; treatment proportion p₁ = 0.985; average p̄ = 0.975.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.2187 = 0.4286.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.2182 = 0.1837.
4. n = (0.4286 + 0.1837)² / (0.0196)² = 975.0, rounded up to 976 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 <- 0.965686274509804                          # control proportion
p1 <- 0.985294117647059                          # 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(297882)
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 = 976 (80% power), 1,305 (90% power)
 75% of observed effect: n per arm = 1,904 (80% power), 2,548 (90% power)
 50% of observed effect: n per arm = 4,662 (80% power), 6,240 (90% power)
power.prop.test: 975 
Simulated power at n = 976 per arm: 0.816 (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 posted analysis compares the two groups using a two-sided t-test and labels the analysis non-inferiority. It reports a 95% confidence level and p > 0.05, but does not post a numerical estimate or confidence limits. That result is distinct from the unadjusted recalculation based on the posted Day 28 summary counts, which gives p = 0.08 and a risk-difference interval that spans zero.

The registry record does not flag a discrepancy between the sponsor result and the recalculation. The two results should still not be treated as interchangeable: the recalculation is a simple unadjusted analysis of summary statistics, while the sponsor’s test may reflect a different analysis method or estimand. The registry record does not provide enough detail to determine the exact reason for any difference in method or result.

The sponsor’s own analysis is the reported trial analysis, but its non-inferiority interpretation cannot be independently checked from the posted details. The non-inferiority margin, analysis population, numerical confidence interval, and relevant protocol details are not reported in the registry record. A p-value above 0.05 from a two-sided test does not by itself establish non-inferiority.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies Cure Rate on Day 28 as the primary outcome and Cure Rate Day 14 as a secondary outcome. It does not report a plan for controlling the chance of false-positive findings across multiple outcomes, time points, or other analyses. Whether the protocol specified a testing hierarchy or another multiplicity strategy is not reported in the registry record. The Day 14 unadjusted result should therefore be read as exploratory context rather than as an independently confirmatory finding.

Missing-data handling is also not reported. The posted outcome counts include group denominators, but the registry record does not explain whether all randomized participants contributed to each outcome, how unavailable Day 28 or Day 14 assessments were classified, or whether any imputation or sensitivity analysis was used. Without these details, the effect of missing outcome data on the estimates cannot be assessed.

The analysis population is not reported in the registry record. It is unclear whether the sponsor’s non-inferiority analysis used all randomized participants, participants treated as assigned, participants who completed follow-up, or a different population. In general, non-inferiority conclusions can be sensitive to the choice of analysis population, so this information is important to evaluating the sponsor’s interpretation.

The record reports randomization and single masking but does not describe the allocation sequence, concealment, masked parties, or departures from assigned treatment. Nor does it report interim analyses or the statistical analysis plan. These are not grounds to assume that procedures were absent; they are details that are not reported in the registry record. Their absence from the record limits independent assessment of how the posted results were obtained.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hemoglobinuria (1.5%), event leading to death (1.0%), blackwater fever (0.5%), hepatitis (0.2%).

The registry reports serious adverse events for 6 participants in the AL group and 3 in the AQ-AS group, with 204 and 612 listed as at risk, respectively. It reports other adverse events for 105 participants in the AL group and 272 in the AQ-AS group. Deaths are listed as 2 in each group. These are counts reported by group; they should not be interpreted as proof that a treatment caused an event or that the groups have equivalent safety.

The top serious-event terms listed in the record are Hemoglobinuria at 1.5%, Event leading to death at 1.0%, Blackwater fever at 0.5%, and Hepatitis at 0.2%. The registry record does not provide further detail about event timing, severity criteria, relatedness to treatment, or whether categories overlap. It also does not give enough information to determine how the listed terms correspond to the group-level serious-event counts.

The brief summary says safety was monitored through clinical examination and biochemical and hematological indices. The posted counts provide a limited description of reported events, not a complete assessment of comparative safety. Their interpretation depends on event definitions, follow-up, ascertainment, and analysis details that are not reported in the registry record.

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

The posted Day 28 outcome records high cure counts in both treatment groups, and the unadjusted comparison does not clearly separate the groups statistically: its confidence interval spans zero and its p-value is 0.08. This describes the observed trial results and their uncertainty. It does not demonstrate that the treatments are identical, and it does not show that any difference is clinically important.

The sponsor labels its analysis non-inferiority, but the registry record does not report the non-inferiority margin or numerical confidence limits. Non-inferiority is a specific claim that depends on ruling out a loss greater than an agreed margin. A non-significant test for any difference is not enough to make that claim. The posted information therefore does not allow an independent statistical verification of the sponsor’s non-inferiority interpretation.

The findings are specific to the trial population, treatment regimens, locations, outcome definitions, and follow-up described in the registry record. The age range is described as 6 months-10 years for the primary outcome population and 6-120 months in the summary. The record’s location descriptions also differ. Generalizing beyond the studied setting requires information not established by the posted results.

The comparison also does not provide a complete account of safety or of the other aims described in the summary. Serious and other adverse-event counts are posted, but details needed to assess event attribution and comparative safety are limited. Molecular markers and gametocyte carriage are described as study aims, while results for these measures are not reported in the registry record.

These data support a cautious reading: the posted primary comparison has uncertainty, the sponsor’s non-inferiority claim cannot be independently assessed from the registry entries, and the secondary result does not resolve the primary uncertainty. The findings are statistical descriptions of trial outcomes, not individual treatment guidance.

18. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be read through its effect estimate and uncertainty, not through event counts or a p-value alone. The Day 28 groups have substantial numbers classified as cured, but the comparative estimate remains uncertain: its confidence interval spans no difference. The distinction between a high observed outcome in both groups and a precise estimate of the difference between them is central to clinical trial interpretation.

It also highlights the difference between a test for any difference and a non-inferiority assessment. Non-inferiority requires a prespecified margin and an analysis capable of showing that the data exclude an unacceptable loss. The record labels the sponsor analysis non-inferiority but does not report the margin or its numerical interval. That makes the claim difficult to evaluate from the registry entry alone.

The differing directions of the primary and secondary estimates show why multiple time points need a clear analysis plan. Secondary outcomes can add context, but unadjusted results can be affected by multiplicity and should not displace the primary endpoint. The record’s missing details about multiplicity, analysis populations, and missing outcomes also demonstrate how reporting quality affects independent assessment.

Finally, the trial record brings together efficacy, safety, and biological aims, but these are not interchangeable forms of evidence. Cure counts, adverse-event summaries, and molecular measures answer different questions. Clear definitions and complete reporting are necessary to interpret each measure and understand how they relate.

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.

Several limitations specific to this registry record restrict interpretation. The location descriptions differ: the brief summary names Banso, Limbe, and Garoua, while the primary outcome description names Mutengene, Bangolan, and Garoua. The record does not explain the discrepancy. The age range is stated in two forms, 6-120 months and 6 months-10 years, and the record does not clarify whether these descriptions reflect different eligibility wording or populations.

The primary endpoint’s protocol-specific cure definition is not reported. Although the summary refers to a WHO standardized 28-day protocol, the registry does not detail the criteria for cure or how reinfection and recrudescence were handled in the primary analysis. The summary mentions molecular analysis of msp1 and msp2 genes for these outcomes, but the relationship between those analyses and the posted cure counts is not described.

The sponsor’s analysis cannot be fully evaluated because the non-inferiority margin, numerical estimate, confidence limits, analysis population, and statistical plan are not reported in the registry record. The recalculated results use posted summaries and are unadjusted; they may not reproduce the sponsor’s method. The record also does not report missing-data procedures, multiplicity control, allocation concealment, who was masked, or whether interim analyses were conducted.

Safety reporting is limited to group counts and selected serious-event terms. Event definitions, treatment relatedness, timing, and possible overlap are not reported. Results for the molecular and gametocyte aims described in the summary are also not reported in the registry record. These are limits of the available record and do not establish what analyses or procedures were performed outside it.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Artemisinin-Based Combination Therapy: Clinical Trials in Cameroon — NCT00297882.
• Registry record last updated 2021-06-08; status last verified 2021-05.
• Results first posted 2021-06-08.
• 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

NCT00297882 is a completed randomized, single-masked, parallel-group Phase III trial sponsored by the London School of Hygiene and Tropical Medicine. It compared artemether-lumefantrine with amodiaquine-artesunate for malaria treatment in children in Cameroon. The registry lists enrollment of 816, a start date of 2006-07, and primary completion in 2009-04.

The primary outcome was cure rate on Day 28; Cure Rate Day 14 was posted as a secondary outcome. The Day 28 recalculated risk-difference interval spans zero, and the unadjusted p-value is 0.08. The sponsor analysis is labelled non-inferiority, but the margin and numerical confidence limits are not reported in the registry record. Missing-data handling, analysis populations, multiplicity procedures, and several protocol details are also not reported, limiting independent assessment.