Optimal Chemopreventive Regimens to Prevent Malaria and Improve Birth Outcomes in Uganda: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Optimal Chemopreventive Regimens to Prevent Malaria and Improve Birth Outcomes in Uganda (NCT04336189), a randomized phase 3 study. The primary outcome is Risk of Having a Composite Adverse Birth Outcome.

2. Clinical Question

The clinical question is broader than whether a regimen changes one specific birth outcome. A participant was counted for the primary endpoint if any listed component occurred. That structure combines outcomes that differ in timing and clinical meaning, from fetal loss to neonatal death, while retaining a single binary endpoint for the main comparison. It also means that the overall composite result cannot identify which component accounts for any observed difference.

The registry describes the trial hypothesis as testing whether SP plus DP reduces adverse birth outcomes compared with SP alone or DP alone. The posted primary comparisons, however, use SP with DP placebo as the reference and give estimates for DP with SP placebo and for SP plus DP. The statistical interpretation should follow those comparisons and the outcome definition rather than treating the stated hypothesis as a reported finding.

3. Trial Design

The registry identifies this as a randomized phase III trial with a sequential model and triple masking. The brief summary describes it as double-blinded. The record does not explain the difference between those masking descriptions, so the masking procedure cannot be characterized more specifically from the registry record alone.

The brief summary states that 2757 HIV-uninfected pregnant women enrolled at 12–20 weeks of gestation were randomized in equal proportions to three intermittent preventive treatment regimens. One group received SP every 4 weeks with DP placebo, one received DP every 4 weeks with SP placebo, and one received SP and DP together every 4 weeks. Placebos were described as being used to support blinding. The arm-specific primary outcome denominators reported are 842, 846, and 850, respectively; the registry does not explain how those analysis denominators relate to the enrollment figure.

The primary outcome timeframe runs from the first dose of study drugs through 28 days postpartum, described as an average of 6 months. The brief summary likewise states that follow-up ended 28 days after birth. The registry lists the trial status as completed, with a start date of 2020-12-28 and a primary completion date of 2024-07-28.

The listed interventions are SP and DP. The record also lists secondary outcomes covering spontaneous abortion, anemia, adverse events, placental malaria, malaria during pregnancy, microscopic parasitemia, and stillbirth. It reports 26 outcome measures, while the posted secondary outcomes number 23. Details of sequence generation, concealment, the rationale for the sequential model, and the trial's original statistical design assumptions are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

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 Risk of Having a Composite Adverse Birth Outcome, measured over Time from first dose of study drugs up to 28 days postpartum, an average of 6 months.

The primary endpoint is the risk of having a composite adverse birth outcome. A participant is counted if any one or more of the defined events occurs: spontaneous abortion, stillbirth, low birth weight, preterm birth, small-for-gestational-age birth, or neonatal death. The definitions use gestational age, birth weight, or weight-for-gestational-age thresholds; the neonatal death component covers death during the first 28 days of life. Threshold signs in the registry definitions correspond to less than 28 weeks for spontaneous abortion, more than 28 weeks for stillbirth, less than 2500 gm for low birth weight, less than 37 weeks for preterm birth, and below the 10th percentile for small-for-gestational-age birth.

As a binary composite, the endpoint gives one overall comparison of whether a participant experienced any listed event. Composite endpoints can be useful when a trial seeks to assess a range of related outcomes through one primary measure. That is a general statistical explanation, not a stated rationale for this trial’s endpoint. The registry does not report why these particular components were combined or how the components were prioritized.

The combined measure has an important interpretive limit: a difference in the composite does not show that every component changed in the same direction, or that one specific component drove the result. Component-specific counts and comparisons would be needed to answer those questions. The primary result also concerns the defined follow-up period, ending 28 days postpartum, rather than outcomes beyond that period.

7. Results Posted in the Registry

• DP + SP placebo every 4 weeks: 30.9% (261/846) versus 26.4% (222/842) on control; risk difference 4.5 percentage points (95% CI 0.2 to 8.8), risk ratio 1.17 (1.01–1.36); unadjusted two-proportion z-test p = 0.041.
• SP + DP given every 4 weeks: 30.0% (255/850) versus 26.4% (222/842) on control; risk difference 3.6 percentage points (95% CI -0.6 to 7.9), risk ratio 1.14 (0.98–1.33); unadjusted two-proportion z-test p = 0.097.

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 Spontaneous Abortion

• 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:
  • DP + SP placebo every 4 weeks: 1.9% (16/846) versus 1.4% (12/842) on control; risk difference 0.5 percentage points (95% CI -0.8 to 1.7), risk ratio 1.33 (0.63–2.79); unadjusted two-proportion z-test p = 0.453.
  • SP + DP given every 4 weeks: 1.5% (13/850) versus 1.4% (12/842) on control; risk difference 0.1 percentage points (95% CI -1.0 to 1.3), risk ratio 1.07 (0.49–2.34); unadjusted two-proportion z-test p = 0.859.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between DP + SP placebo every 4 weeks and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between SP + DP given every 4 weeks and the control. The interval gives the range of effects that remain compatible with the data.

Incidence of Grade 3-4 AEs Possibly Related to Study Drugs

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • DP + SP placebo every 4 weeks: 29.00 versus 50.00 (Events per person-years) on control; rate ratio 0.58 (95% CI 0.55–0.61, approximate, Poisson model); p ≈ <0.001.
  • SP + DP given every 4 weeks: 41.00 versus 50.00 (Events per person-years) on control; rate ratio 0.82 (95% CI 0.78–0.86, approximate, Poisson model); p ≈ <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically lower for DP + SP placebo every 4 weeks than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically lower for SP + DP given every 4 weeks than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Risk of Placental Malaria

• 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:
  • DP + SP placebo every 4 weeks: 40.8% (324/795) versus 60.8% (472/776) on control; risk difference -20.1 percentage points (95% CI -24.9 to -15.2), risk ratio 0.67 (0.61–0.74); unadjusted two-proportion z-test p = <0.001.
  • SP + DP given every 4 weeks: 50.1% (393/784) versus 60.8% (472/776) on control; risk difference -10.7 percentage points (95% CI -15.6 to -5.8), risk ratio 0.82 (0.75–0.90); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for DP + SP placebo every 4 weeks than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for SP + DP given every 4 weeks than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes span several kinds of endpoints: participant counts, event rates, pregnancy malaria measures, anemia, and birth outcomes. Their overall pattern is not uniform in statistical form or follow-up definition. Some address events during pregnancy or through delivery, while another covers study-drug exposure through 28 days postpartum. Those distinctions matter when comparing secondary findings with the primary composite, which uses its own specified period and combines multiple birth outcomes.

At a broad level, the secondary outcomes provide context for the trial’s clinical domains, including malaria-related outcomes and safety, but they do not replace the primary endpoint. A result on placental malaria or an adverse-event rate does not establish the effect on the composite birth outcome. Likewise, the composite cannot explain a secondary outcome or identify which component contributed to it. These outcomes can be considered alongside the primary result as related but distinct evidence.

The registry posts unadjusted comparisons for selected secondary outcomes, while its reported-analyses listings do not provide formal analyses for those outcomes. No multiplicity adjustment is reported. When many outcomes are examined, the chance of at least one apparently unusual result can increase, even if there is no underlying effect for any of them. This is a general statistical concern, not a claim about what occurred in this trial. Unadjusted secondary findings therefore carry less confirmatory weight than a prespecified primary analysis with a reported multiplicity strategy.

The registry does not report which secondary outcomes were designated as confirmatory, how their order of importance was set, or whether their analyses were planned before results were examined. Their findings are best treated as descriptive or exploratory signals in the context of the posted record, rather than as independent confirmation of the primary result. Specific secondary estimates and intervals should be interpreted on their own endpoint scales and with attention to the uncertainty and reporting gaps for each outcome.

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

• Number of Participants With Spontaneous Abortion
• Incidence of Anemia Adverse Event Per Time at Risk
• Incidence of Grade 3-4 AEs Possibly Related to Study Drugs
• Risk of Placental Malaria
• Incidence of Malaria During Pregnancy
• Microscopic Parasitemia During Pregnancy
• Prevalence of Anemia During Pregnancy
• Stillbirth

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a binary participant-level measure: the registry reports counts of participants with the composite event in each arm. A binary endpoint records whether the event occurred, rather than how many separate component events one participant experienced. The comparison statistic is a risk difference, which expresses the difference between the two reported event risks. A value of zero corresponds to no difference in risk; positive values mean the comparison group’s risk is higher than the reference group’s risk, and negative values mean it is lower.

What does the confidence interval describe?

A confidence interval conveys the uncertainty around an estimated effect under the statistical method used to produce it. For the primary risk differences, the interval gives a range of values compatible with the posted estimate and method. If that range includes zero, the data are compatible with no risk difference as well as with differences in either direction covered by the interval. If it excludes zero, the interval is inconsistent with a zero difference at the corresponding confidence level, subject to the assumptions of the analysis. An interval is not a guarantee that the true value lies inside it, and it does not represent the range of outcomes for individual participants.

The primary comparisons also include unadjusted p-values. A p-value describes how unusual data at least as incompatible with the null hypothesis would be if the null hypothesis and the statistical assumptions held. It is not the probability that the null hypothesis is true, nor is it a measure of effect size. A p-value below a chosen threshold does not by itself establish clinical importance. The registry record does not report a formal multiplicity adjustment or a sponsor-reported analysis plan for these comparisons, so the posted p-values should be interpreted as unadjusted.

Why distinguish risks, risk differences, and rate ratios?

The primary endpoint is reported as a risk and compared with risk differences. Risks concern whether participants experienced an event over the stated outcome period. A risk difference is an absolute contrast on that risk scale. Relative measures such as risk ratios and odds ratios can express contrasts on different scales, but they answer different mathematical questions and should not be substituted for the risk difference. The registry also posts relative measures for the primary comparison; the risk-difference interpretation above follows the comparison metric reported for the primary endpoint.

Some secondary outcomes are event counts or rates rather than binary participant outcomes. For example, the grade 3–4 adverse-event outcome is labelled as events per person-years and has rate-ratio comparisons. A rate uses event counts in relation to time at risk, so it is not interchangeable with the proportion of participants who experienced at least one event. One participant may contribute more than one event to a count-based rate outcome. The registry’s posted rate comparison is marked as Poisson-based; it does not report a dispersion parameter or a different model specification.

In general, Poisson methods model event counts relative to exposure time. A key general consideration is whether the observed variation in counts is adequately represented by the model; over-dispersion, meaning more variation than the model assumes, can make standard errors and confidence intervals too small if not addressed. The registry record does not report a diagnostic for over-dispersion, an alternative model, or a detailed rate-analysis plan. This general consideration should not be taken to mean over-dispersion occurred in this trial.

What is not specified about the analysis?

The registry record does not report the primary model, covariates, handling of missing outcome data, analysis population, or whether any formal interim analyses occurred. It also does not identify an intention-to-treat or per-protocol population for the posted primary results. Random allocation is reported, but the details of allocation generation and concealment are not reported in the registry record. Those omissions limit how fully the analysis can be reproduced or assessed from the registry alone.

The statistical comparisons should consequently be read as posted summaries, with the stated outcome definitions and denominators. No unreported adjustment or assumption should be attributed to them. The record reports no analyses for the posted secondary outcomes, while providing summary comparisons for several outcomes; those summaries do not supply the missing detail about methods or multiplicity control.

11. Confidence Intervals and Precision

The confidence intervals quantify uncertainty in the estimated comparisons, not certainty about the treatment effect. For the DP regimen compared with SP, the primary risk difference is 0.045, with a 95% confidence interval from 0.002 to 0.088. This interval is entirely above zero, but its width indicates that the estimate is not a single precisely known value. The corresponding unadjusted p-value is 0.041.

For SP plus DP compared with SP, the risk difference is 0.036, with a 95% confidence interval from -0.006 to 0.079. Because this interval crosses zero, the posted summary leaves uncertainty about whether the composite risk differs from the SP reference group and in which direction. The interval also includes positive differences, so a non-significant result should not be read as proof of equivalence or no effect. The p-value for this comparison is 0.097.

These intervals are based on the posted group summaries and describe uncertainty in the comparison, not variation between participants or the range of individual experiences. They also do not address possible biases arising from missing data, deviations from the assigned regimen, or analysis choices that are not described in the registry record. No adjusted confidence intervals are reported.

Precision is endpoint-specific. The primary composite combines several different outcomes, and its interval does not show how precisely any individual component was estimated. The registry provides component-related secondary outcomes, but not every component is accompanied by a reported comparison analysis. The confidence intervals should therefore be used to assess uncertainty in the stated composite comparisons, not to infer precision for each event category or for a direct comparison between the two active regimens.

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.

Sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculations. For binary participant outcomes, the figures are participants per arm. For time-to-event displays, the stated convention is total events. The illustration uses a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under its assumptions. The 90% power column uses a higher target chance of detection, so it generally requires more participants for the same assumed effect. These are design-planning quantities, not a measure of how likely the completed trial was to find a result after observing its data.

For example, planning for 100% of the observed primary effect in the DP-versus-SP comparison gives 1,593 participants per arm for 80% power and 2,132 participants per arm for 90% power. Planning for 75% of the observed effect gives 2,799 participants per arm for 80% power and 3,746 participants per arm for 90% power. The analogous combined-regimen comparison gives 2,405 participants per arm for 80% power and 3,219 participants per arm for 90% power when planning for 100% of its observed effect.

Smaller effects are harder to distinguish from random variation, so the illustrations require more participants when the assumed effect is a smaller fraction of the observed effect. These figures are not observed power. They are conditional planning examples and should not be interpreted as evidence that the trial was adequately or inadequately powered for its original objectives.

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 = 0.264; treatment proportion p₁ = 0.309; average p̄ = 0.286.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6391 = 1.2527.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6383 = 0.5372.
4. n = (1.2527 + 0.5372)² / (0.0449)² = 1,592.5, rounded up to 1,593 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 <- 0.263657957244656                          # control proportion
p1 <- 0.308510638297872                          # 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(4336189)
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 = 1,593 (80% power), 2,132 (90% power)
 75% of observed effect: n per arm = 2,799 (80% power), 3,746 (90% power)
 50% of observed effect: n per arm = 6,220 (80% power), 8,327 (90% power)
power.prop.test: 1592.5 
Simulated power at n = 1,593 per arm: 0.798 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary composite outcome and numerous secondary outcomes, with 26 outcome measures reported overall and 23 posted secondary outcomes. It does not report a multiplicity-control procedure for the two primary comparisons or for the set of secondary comparisons. When researchers test multiple hypotheses, the probability of obtaining at least one small p-value by chance can rise. Adjustments or a clearly specified testing hierarchy can help control that issue, but no such approach is described in the registry record.

The two primary comparisons are each presented against the SP reference group. The record does not state whether a particular comparison was designated as the sole confirmatory contrast, whether both were intended to be tested at the same inferential level, or how any multiplicity would be handled. The unadjusted p-values should therefore not be treated as multiplicity-adjusted evidence. This does not change the numerical results; it limits the strength of claims that can be based on isolated thresholds.

Important details about missing data and analysis populations are also not reported in the registry record. The record does not explain how participants with missing birth outcomes, incomplete follow-up, or other unavailable measurements were handled. It does not identify whether the primary analysis followed intention-to-treat, per-protocol, or another population definition. Nor does it report sensitivity analyses assessing the impact of missing observations or departures from assigned treatment.

The arm-specific denominators differ across some posted endpoints, but the registry does not explain the reasons for those denominator differences. They should not be attributed to missingness, exclusions, or any other specific process without further information. Details of allocation concealment, adherence handling, and a prespecified statistical analysis plan are also not reported. These gaps make it difficult to assess the robustness of the findings to analysis choices or to reconstruct the intended inferential framework from the registry record alone.

15. 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: congenital anomoly (1.4%), anemia (0.9%), neutropenia (0.4%), pre-eclampsia (0.3%), post-partum hemmorrha (0.3%).

The serious adverse event summary reports participants at risk and participants affected for each regimen, along with deaths. For SP with DP placebo, the serious-event figures are 896 at risk and 25 affected, with 1 death. For DP with SP placebo, the figures are 902 at risk and 26 affected, with 2 deaths. For SP plus DP, they are 908 at risk and 27 affected, with 0 deaths. These counts describe the registry’s reported safety summary; they are not a comparison adjusted for exposure time or participant characteristics.

The listed serious-event terms include congenital anomoly, anemia, neutropenia, pre-eclampsia, post-partum hemmorrha, and puerperal sepsis, with percentages reported for those terms. The record does not describe the event-classification method, causal adjudication process, or whether participants could contribute to more than one term. The primary composite outcome is a separate endpoint and should not be conflated with the serious adverse event summary.

The safety denominators differ from the primary outcome arm denominators. The registry does not explain that difference, so no reason for it can be inferred from these summaries. Counts alone also do not establish comparative safety or causation.

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

The posted primary results describe unadjusted comparisons of a composite adverse birth outcome between each active regimen and the SP reference regimen. For DP with SP placebo, the risk difference is positive and its confidence interval excludes zero. For SP plus DP, the estimated difference is also positive, but its interval includes zero. These findings describe the observed summaries and their statistical uncertainty; they do not by themselves establish a clinically important difference or a treatment effect for every component of the composite.

A result that does not meet a conventional statistical threshold is not proof that two regimens are equivalent. The interval for the combined regimen remains compatible with values on either side of zero, and the registry does not report an equivalence or non-inferiority framework. Conversely, a p-value below a threshold does not establish that a difference is large enough to matter clinically. The registry record does not state a clinically important difference threshold for the primary endpoint.

The composite outcome includes spontaneous abortion, stillbirth, low birth weight, preterm birth, small-for-gestational-age birth, and neonatal death. Because those events differ, an aggregate comparison does not identify which component accounts for the overall result. Component-specific estimates and a prespecified approach to interpreting them would be needed to make more specific claims. No direct comparison between DP alone and SP plus DP is posted.

The interpretation is also limited to the trial population and outcome period described in the registry: HIV-uninfected pregnant women enrolled at 12–20 weeks of gestation, with follow-up through 28 days postpartum. The record does not support extending the findings to populations, settings, or follow-up periods not described. Missing-data handling, analysis populations, and multiplicity procedures are not reported, which leaves uncertainty about how those choices might affect inference.

Accordingly, the posted data support a cautious statistical reading of the two comparisons, not medical advice or a recommendation. The registry record alone does not establish why the observed patterns occurred, whether they would be reproduced in another study, or how the balance of benefits and harms should be judged clinically.

17. Why This Trial Matters Statistically

This trial illustrates why a clinical outcome and its statistical scale must be read together. The primary endpoint is a binary composite that combines several adverse birth outcomes, while the posted contrasts are risk differences against a common reference group. The risk difference gives an absolute comparison on the outcome’s risk scale, and its confidence interval conveys uncertainty around that comparison. Keeping the endpoint definition and estimate scale in view prevents a broad composite result from being mistaken for a component-specific finding.

The two primary comparisons also demonstrate why a point estimate alone is not enough. The DP-alone estimate has an interval that excludes zero, whereas the combined-regimen interval crosses zero. That distinction is informative about the uncertainty represented by the posted analyses, but it does not test whether the active regimens differ from each other. A direct contrast would be required for that question. Nor does a threshold-based p-value resolve clinical importance.

The registry’s collection of secondary outcomes emphasizes that trials often measure outcomes on different scales and over different periods. A participant-level risk, an event rate, and an outcome measured at delivery require distinct interpretations. Their results may provide context, but they do not automatically reinforce the primary endpoint, especially when the record does not report a hierarchy or multiplicity strategy.

Finally, this record shows the value of transparent statistical reporting. Details about the analysis population, missing data, adjustment, and original sample-size rationale are not reported. Without those details, readers can interpret the posted estimates and intervals but cannot fully reconstruct the planned inferential approach. Distinguishing what the posted comparisons quantify from what remains undocumented is central to a careful reading of clinical trial evidence.

18. Limitations

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

Several limitations specific to this registry record constrain interpretation. The primary outcome is a composite of events with different definitions and timing. The posted overall comparison cannot identify which component contributed to the result, and the record does not report the rationale for combining the components or a hierarchy among them.

The analysis details are incomplete. The registry does not report the primary statistical model, covariate adjustment, handling of missing observations, or the analysis population. It also does not state how treatment adherence or deviations from the randomized regimen were handled. The primary outcome denominators differ by arm, and the record does not explain the relationship between those denominators and enrollment or the reasons for any endpoint-specific denominators.

The registry identifies triple masking, while the brief summary calls the trial double-blinded; no explanation reconciles those descriptions. The record also does not report allocation concealment details, the original sample-size justification, or whether interim analyses were conducted. The planning illustrations based on observed effects cannot fill those gaps or reconstruct the trial’s design assumptions.

Multiplicity is another limitation: no adjustment or testing hierarchy is reported for the primary comparisons and multiple secondary outcomes. Secondary comparisons are therefore less suitable as confirmatory evidence. The record does not report direct comparison of DP alone with the combined regimen, so the posted pairwise estimates against SP cannot answer whether those two active regimens differ from one another.

These limitations concern what can be established from the registry record. They do not show that any particular bias or analysis problem occurred, but they restrict independent assessment of robustness and reproducibility.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Optimal Chemopreventive Regimens to Prevent Malaria and Improve Birth Outcomes in Uganda — NCT04336189.
• Registry record last updated 2025-11-06; status last verified 2025-06.
• Results first posted 2025-11-06.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed randomized phase III trial of intermittent preventive treatment during pregnancy in Uganda. HIV-uninfected pregnant women enrolled at 12–20 weeks of gestation were assigned to SP, DP, or SP plus DP regimens administered every 4 weeks. The primary endpoint was a composite adverse birth outcome assessed through 28 days postpartum.

The posted primary comparisons use SP with DP placebo as the reference group. The DP regimen has a risk difference of 0.045, with a 95% confidence interval from 0.002 to 0.088 and an unadjusted p-value of 0.041. The combined regimen has a risk difference of 0.036, with a 95% confidence interval from -0.006 to 0.079 and an unadjusted p-value of 0.097.

The registry record does not report a multiplicity procedure, detailed primary analysis plan, analysis population, or missing-data approach. The posted estimates should be interpreted as unadjusted comparisons of the defined composite, with their uncertainty and reporting limitations kept in view.