Task-shifted Adaptation of the WHO-PEN Intervention to Address Cardio-metabolic Complications in People Living With HIV in Zambia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Task-shifted Adaptation of the WHO-PEN Intervention to Address Cardio-metabolic Complications in People Living With HIV in Zambia (NCT05005130), a randomized na study. The primary outcome is Change in Percent of Participants With Dual HIV and Blood Pressure Control.

2. Clinical Question

3. Trial Design

The registry describes a randomized, unmasked, crossover study. The intervention was TASKPEN, and the comparator was standard of care. The study was registered as a pilot of a task-shifted adaptation of the WHO Package of Essential Noncommunicable Disease Interventions for integrated HIV and noncommunicable disease services in Zambia. The registry lists the study as completed, with a start date of 2021-09-20 and primary completion on 2022-12-23.

The two cluster descriptions specify different periods without and with TASKPEN. Cluster 1 (George) had 3 months without TASKPEN followed by 6 months with TASKPEN; Cluster 2 (Chilengi) had 6 months without TASKPEN followed by 3 months with TASKPEN. The record labels the design crossover, but does not state whether the clusters themselves were the randomized units, how allocation was generated, or how period and cluster effects were handled in the analysis. It also does not report a washout period or explain whether one was used.

The primary outcome is defined from baseline to 6 months, while the posted arm results are labeled standard of care and TASKPEN. The record does not explain how that endpoint timeframe was reconciled with the differing cluster periods, or how crossover observations were incorporated into the posted comparison. The posted primary outcome counts are 634 for standard of care and 456 for TASKPEN; these are outcome-specific group counts, not a description of the crossover analysis population.

The registry lists enrollment of 1129. Its primary outcome description states that eleven participants with incomplete data were excluded. It does not report the original sample-size justification, the target recruitment by cluster, or the trial’s own planned statistical analysis. No analyses are listed in the registry’s analysis field. Consequently, the posted between-group results can be described as registry-reported comparisons, but their relationship to a randomized crossover estimand is not fully documented.

4. Participant Flow and Accounting

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

Before assignment: 28 Healthcare Providers and 1101 patient participants were enrolled and 11 were excluded from the analysis. This 'mini' stepped wedge pilot had 2 clinic clusters to establish approach feasibility. In a stepped wedge fashion, participants at both clinics were surveyed at baseline and then one site was randomly selected to receive the intervention for 3 months. A midline survey was then conducted and the second site was switched to the intervention before an endline survey 3 months later.

Time Period 1 Baseline (T0)

Time Period 2 Midline Survey (T1)

Time Period 3 Endline Survey (T2)

Analysis population for the primary outcome, as defined in the registry: Eleven patient participants with incomplete data were excluded.

5. Baseline Characteristics

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

Population: Data are reported for those patient participants who had complete primary outcomes.

6. Primary Endpoint

The registry lists the primary outcome as Change in Percent of Participants With Dual HIV and Blood Pressure Control, measured over Baseline to 6 months.

The primary endpoint is the change in the percent of participants with dual HIV and blood pressure control from baseline to 6 months. It combines control of HIV with control of blood pressure, so it represents achievement of both components rather than either component alone. For HIV, the description specifies an HIV RNA level below 1000 copies per mL on the most recent measure. For participants with missing viral-load results, the dual-control definition refers to evidence of 6MMD. The registry does not expand that abbreviation.

For blood pressure, the dual-control definition specifies systolic blood pressure below 140 mmHg and diastolic blood pressure below 90 mmHg. There is a wording difference within the registry description: the initial measurement sentence refers to systolic blood pressure below 140 mmHg and/or diastolic blood pressure below 90 mmHg, whereas the parenthetical dual-control definition uses AND between those criteria. The record does not clarify this difference.

A combined endpoint can be useful for describing whether participants meet a set of related clinical targets at the same time. It also has an interpretive trade-off: the combined percentage does not show which component accounts for a change in the overall measure. Separate component outcomes can help characterize that pattern, but the primary endpoint remains the joint definition. The registry says eleven participants with incomplete data were excluded from this endpoint; it does not give further details about missing-data handling.

7. Results Posted in the Registry

• TASKPEN: 60.1% (274/456) versus 52.1% (330/634) on control; risk difference 8.0 percentage points (95% CI 2.1 to 14.0), risk ratio 1.15 (1.04–1.28); unadjusted two-proportion z-test p = 0.008.

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 Trained Healthcare Providers (Intervention Reach)

• 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:
  • Cluster 2 Healthcare Providers (Chilenje): 63.2% (60/95) versus 85.3% (29/34) on control; risk difference -22.1 percentage points (95% CI -37.5 to -6.8), risk ratio 0.74 (0.60–0.91); unadjusted two-proportion z-test p = 0.017.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Cluster 2 Healthcare Providers (Chilenje) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Changes in HIV Disease Control, as Measured by the Percent of Patient Participants With HIV RNA Suppression (Defined as <1,000 Copies/mL)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • TASKPEN: 88.9% (361/406) versus 85.1% (461/542) on control; risk difference 3.9 percentage points (95% CI -0.4 to 8.1), risk ratio 1.05 (1.00–1.10); unadjusted two-proportion z-test p = 0.083.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TASKPEN and the control. The interval gives the range of effects that remain compatible with the data.

Intervention Cost Per Patient

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • TASKPEN: mean 287.50 versus 352.53 on control; difference -65.03 (95% CI -268.45 to 138.39), standardized effect d = -0.21; z-test p = 0.531.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TASKPEN and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover distinct parts of the intervention’s purpose: implementation reach and adoption, HIV disease control, acceptability, appropriateness, feasibility, and cost. These outcomes are related to the primary endpoint because they help describe whether TASKPEN was delivered and whether service outcomes changed. They are not alternate versions of the primary endpoint. A program can show a pattern in implementation outcomes that differs from its pattern in a combined clinical outcome, and a change in one domain does not establish a change in another.

The posted secondary results do not form a uniformly consistent signal across every domain. The reach comparison is between healthcare provider clusters, whereas HIV suppression is a patient outcome and cost is a mean-valued measure. Their units, populations, and timeframes are different. As a result, a simple vote-counting approach—treating each result as an equivalent positive or negative test—would be misleading. The outcomes should be interpreted according to their individual definitions and uncertainty, and in relation to the pilot’s implementation aims.

The registry lists seven secondary outcomes but posts results for only some of those measures in the recorded outcomes summarized in this analysis. It lists no reported analyses. Results for acceptability, appropriateness, feasibility, and clinic adoption are therefore not available as inferential comparisons in the posted analysis record, even though those topics appear among the secondary outcomes.

Unadjusted secondary results carry less weight as confirmatory evidence when multiple outcomes are examined. Each additional statistical comparison creates more opportunities for apparently notable results to occur by chance. A multiplicity strategy can control the overall error rate or distinguish confirmatory outcomes from exploratory ones, but the registry does not report such a strategy. It also does not provide a hierarchy or prespecified analysis plan for the secondary outcomes. The secondary p-values should therefore be treated as exploratory signals rather than as independent confirmation of the primary finding.

The primary endpoint remains the central clinical comparison, while the secondary outcomes provide context about service reach, other health measures, and costs. Their different patterns neither invalidate nor independently verify the primary result. They instead indicate that interpretation should consider the full set of domains, the limited analysis information, and the uncertainty around each estimate.

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

• Number of Clinics That Adopted the Intervention (Intervention Adoption)
• Number of Trained Healthcare Providers (Intervention Reach)
• Changes in HIV Disease Control, as Measured by the Percent of Patient Participants With HIV RNA Suppression (Defined as <1,000 Copies/mL)
• Change in Intervention Appropriateness
• Change in Intervention Acceptability
• Change in Intervention Feasibility
• Intervention Cost Per Patient

9. Statistical Interpretation

10. Statistical Methods Explained

What does a percentage outcome represent?

The primary endpoint is a binary outcome summarized as a percentage: each participant either meets the joint definition of dual control or does not. The group percentage therefore describes how often the defined outcome was recorded among participants represented in that group. It does not describe the degree of blood pressure or viral-load control among those who do not meet the combined definition. Because the endpoint requires both HIV and blood pressure criteria, a participant who meets one component but not the other does not meet the joint endpoint.

Binary outcomes can be compared using several measures. A risk difference expresses the absolute difference between group proportions. A risk ratio compares the proportions as a ratio, while an odds ratio compares the odds of the outcome. Each uses a different scale, so the numerical values are not interchangeable. The posted primary comparison reports a risk difference, and additional relative measures are available in the statistical results. The registry does not state which measure was prespecified as the principal inferential measure beyond naming the primary outcome.

Why distinguish descriptive results from adjusted analyses?

Group percentages and unadjusted comparisons summarize the posted observations without necessarily accounting for all design features. In a crossover study, outcomes can be affected by the period in which a group receives an intervention, the order of periods, and the cluster or site. Repeated measurements may also be correlated: outcomes from the same participant or clinic are often more alike than outcomes from unrelated units. Treating correlated observations as independent can make uncertainty appear smaller than it is. An analysis can address such structure through methods matched to the design, but the registry does not report whether those methods were used for the posted comparisons.

Randomized allocation can help make groups comparable on average when allocation is properly implemented and the analysis follows the design. However, the registry’s description does not identify the randomization unit or explain the analysis population. The labels “Cluster 1” and “Cluster 2” describe the settings and sequences, while the primary outcome is posted under standard-of-care and TASKPEN groups. That reporting does not by itself reveal how allocation, crossover, or repeated observations were handled.

How should a p-value be understood?

A p-value is calculated under a null hypothesis and specified statistical assumptions. It measures how unusual the observed data, or data more extreme, would be under that null model. A smaller value can be evidence against the null comparison when the model and analysis are appropriate. It is not the probability that the null hypothesis is true, and it does not quantify the probability that an intervention will benefit an individual. It also does not measure clinical importance. The primary unadjusted p-value should be considered alongside the estimated difference, its interval, the endpoint definition, and the limitations in the reported design analysis.

Unadjusted means the comparison is not presented as adjusted for covariates or design factors in the registry results. It does not necessarily mean that no adjustment was performed elsewhere; it means that an adjusted result is not reported in this record. The registry lists no reported analyses, so further model specifications, standard errors, and any adjustment procedures are not available.

What does a confidence interval add?

A confidence interval conveys uncertainty around an estimate. In repeated use of a valid procedure, intervals constructed at a stated confidence level would cover the underlying quantity at the corresponding long-run rate. For an individual study, it provides a range of effect values compatible with the estimate and the analysis assumptions. A narrow interval indicates greater precision than a wide interval, while an interval spanning the null value indicates that the data do not clearly distinguish the estimate from that null value at the corresponding level. These interpretations depend on the validity of the analysis, including how clustering and crossover are handled.

For the primary risk difference, the posted interval is entirely on the positive side of zero. That describes the direction and statistical uncertainty of the registry’s unadjusted estimate. It does not correct for unreported design features, missing data, or multiple outcome testing. The interval should not be read as a guarantee that the true effect lies within its endpoints.

Why do endpoint definitions and denominators matter?

The primary outcome combines HIV and blood pressure information, and its definition includes a special rule for participants with missing viral-load results. The record also notes exclusion of eleven participants with incomplete data. These details affect which participants can meet the endpoint and how the measured percentage should be interpreted. The registry does not report whether missingness differed by group, how missing values were otherwise handled, or whether excluded participants differed from those retained.

The group denominators vary across outcomes. That is expected when outcomes require different measurements or use different analysis populations, but the record does not explain every denominator difference. Outcome-specific counts should not be treated as a single common analytic population. In particular, a posted percentage for one endpoint cannot be assumed to refer to exactly the same participants as a percentage for another endpoint.

The primary description also uses “and/or” in its initial blood pressure measurement sentence and “AND” in its parenthetical definition of dual control. Since the difference affects who qualifies, the precise operational rule matters. The registry does not resolve the wording, so the result should be understood according to the recorded definition while recognizing this ambiguity.

What can the record support?

The record supports reporting the posted estimates, group percentages, confidence intervals, and unadjusted p-values as registry results. It does not support reconstruction of an unreported model, an assumption about the original sample-size justification, or a claim that the crossover analysis was properly adjusted. General statistical principles can explain why those details matter, but they cannot fill in missing methods. The posted findings are best treated as descriptive and exploratory evidence from a pilot and formative study, with precision and design limitations made explicit.

11. Confidence Intervals and Precision

The primary outcome percentages are 52.0% for standard of care and 60.0% for TASKPEN. The posted risk-difference interval is entirely above zero, so the unadjusted estimate is compatible with a positive difference. The interval nevertheless spans a range of possible effect sizes; it does not identify a single precise value. Its width represents sampling uncertainty under the analysis used, and its interpretation depends on whether the analysis accounts for the crossover and cluster structure.

A confidence interval is not a range that contains a fixed percentage of individual participant outcomes. It is an uncertainty interval for the estimated group comparison. In general, a narrower interval indicates a more precise estimate, while a wider interval leaves more plausible values unresolved. The registry does not report the confidence level in the posted endpoint description, so the level should not be inferred from the interval alone.

The primary p-value, 0.008, and the confidence interval address related but different aspects of inference. The p-value summarizes compatibility with a null comparison under the test assumptions. The interval conveys the direction and range of compatible effect values. Neither indicates the probability that the intervention has a particular effect, and neither resolves missing analysis details.

Precision varies across the secondary outcomes. The HIV suppression comparison has an interval that crosses the null difference, and the cost comparison has a wide interval spanning both negative and positive mean differences. Such intervals indicate that the posted estimates leave substantial uncertainty about the magnitude and, in some cases, direction of the underlying comparison. The group counts, outcome definitions, and analysis methods also differ across endpoints, so precision should be considered separately for each outcome.

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 illustrations based on observed effects, not the trial’s original design calculations. The registry’s stated illustration assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The original sample-size justification and original design assumptions are not reported in the registry record.

For these binary and continuous outcome illustrations, the figures are participants per arm, not total participants. The record’s note about total events applies to time-to-event calculations; no time-to-event outcome is among the posted planning illustrations. The columns for 80% and 90% power indicate the number of participants per arm estimated to be needed, under the stated assumptions, for the study to have the corresponding chance of detecting the specified effect if that effect were real. Higher planned power generally requires more participants under otherwise unchanged assumptions.

Each planning row uses a different fraction of the observed effect. Planning for 100% of the observed effect assumes a target as large as the effect measured in this pilot; planning for 75% or 50% assumes a smaller target. Smaller effects are harder to distinguish from random variation and therefore require more participants. The displayed figures are not observed power and should not be read as a retrospective measure of whether the completed study was adequately powered.

These calculations are simplified planning aids. They assume equal allocation and a normal approximation, while the registry describes a cluster crossover study. They do not, as presented, account for possible clustering, repeated measurements, crossover periods, incomplete outcome data, or other design complications. Thus the figures help illustrate how detectable effect size relates to planning requirements, but they are not a substitute for a design calculation matched to the trial’s actual structure.

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 = 0.521; treatment proportion p₁ = 0.601; average p̄ = 0.561.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7019 = 1.3757.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6996 = 0.5888.
4. n = (1.3757 + 0.5888)² / (0.0804)² = 597.4, rounded up to 598 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 <- 0.520504731861199                          # control proportion
p1 <- 0.600877192982456                          # 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(5005130)
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 = 598 (80% power), 800 (90% power)
 75% of observed effect: n per arm = 1,068 (80% power), 1,429 (90% power)
 50% of observed effect: n per arm = 2,413 (80% power), 3,230 (90% power)
power.prop.test: 597.4 
Simulated power at n = 598 per arm: 0.803 (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 lists a primary outcome and several secondary outcomes, but does not report a multiplicity plan. When a study evaluates multiple outcomes or comparisons, the chance of at least one nominally notable result can rise if each is interpreted as a separate confirmatory test. Common approaches include designating a primary outcome for the principal inference, adjusting significance thresholds, or clearly labeling other comparisons as exploratory. Which approach, if any, was used is not reported in the registry record. Accordingly, the primary result is distinguishable by its registry designation, but the unadjusted secondary p-values should not be treated as a set of confirmatory findings.

The record reports zero analyses in its analysis listing and no reported secondary analyses. It does not describe a prespecified statistical analysis plan, model, covariate adjustment, handling of clustering, treatment-period effects, or correlation from repeated observations. It also does not provide information about interim analyses. These items are not reported in the registry record, so assumptions about their presence or absence would be unwarranted.

For the primary endpoint, the record explicitly states that eleven participants with incomplete data were excluded. It does not specify what data were incomplete, how the missingness was distributed across the comparison groups, or whether missingness was related to outcome status. The definition permits evidence of 6MMD to be used for participants with missing viral-load measurements, but the record does not explain how often this rule was applied or whether it resolved all missingness. No sensitivity analysis is reported.

The analysis population is also not fully described. The registry does not state whether the primary comparison followed an intention-to-treat principle, whether participants were analyzed according to the assigned sequence, or how switching between standard care and TASKPEN was represented. The posted group counts differ by outcome, and the record does not give a complete accounting of those denominators. These limitations affect both the interpretation of the estimates and confidence in their reported precision.

These gaps do not change the values recorded for the outcomes, but they constrain what can be concluded from them. A transparent account of the planned comparisons, analysis populations, missing-data approach, and multiplicity handling would be needed for a more complete assessment of confirmatory evidence.

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 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports serious adverse events as zero affected participants in both groups. The serious-event at-risk counts are 636 for standard of care and 465 for TASKPEN. It also reports deaths of 4 in standard of care and 1 in TASKPEN. Other adverse events affected 158 participants in the standard-of-care group and 222 in the TASKPEN group, with at-risk counts of 636 and 465, respectively.

These are descriptive counts. The record does not list serious-event terms, and the absence of reported serious events does not establish that no events occurred outside the registry’s reported classification or observation period. The record does not explain whether adverse-event reporting was collected over the same exposure time in each group, how events were attributed during the crossover periods, or whether all participants had equivalent follow-up. The group counts therefore should not be converted into a comparative safety claim.

Safety counts also cannot be interpreted in isolation from study size, follow-up, event definitions, and ascertainment. The registry does not report a formal safety analysis or comparative uncertainty estimates. These figures describe what the record posts; they do not establish that either group is safer.

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

The posted primary outcome shows a higher percentage meeting the registry’s dual-control definition in the TASKPEN group than in standard of care. The unadjusted p-value and confidence interval indicate that the posted difference is not centered on no difference under that comparison. This is evidence about the recorded group summaries, not a complete causal estimate from the crossover design.

The result does not establish that TASKPEN caused the observed difference. The registry does not report how the analysis addressed cluster membership, periods, sequence, or repeated observations, and does not identify the analysis population. The primary endpoint also combines HIV and blood pressure criteria, so its overall percentage does not show which component contributed to the group pattern. The record’s differing wording for the blood pressure rule adds uncertainty about the exact operational definition.

The result does not show that every participant meeting one component also met the other, nor does it describe changes in the continuous values of blood pressure or viral load. It is a percentage meeting a defined joint threshold. The special rule for missing viral-load results and the exclusion of participants with incomplete data further shape what the measure represents.

The secondary outcomes do not resolve these uncertainties. Implementation measures, HIV suppression, and cost address different questions and have different denominators and precision. Their results can provide context, but they are not proof that the primary comparison is unbiased or that the same pattern applies to other clinics or populations. The registry does not report a multiplicity plan, so secondary p-values should be interpreted cautiously.

Finally, a pilot and formative study can inform questions about adaptation, feasibility, delivery, and future evaluation, but the posted record does not establish broad applicability or long-term effects. The findings describe the observed outcomes in this study and the uncertainty around the comparisons as reported. They should not be interpreted as individualized medical guidance or as a definitive determination of treatment effect.

17. Why This Trial Matters Statistically

This study is statistically interesting because it combines an implementation-focused intervention with a clinical endpoint in a randomized crossover design. TASKPEN was intended to adapt and task-shift integrated HIV and noncommunicable disease services, so questions about delivery and reach sit alongside questions about dual control. A single clinical percentage cannot capture every part of that implementation process.

The design makes the missing analysis details especially consequential. Crossover and clustering can create dependencies and period effects that affect estimated uncertainty. The registry provides group summaries and unadjusted comparisons, but does not explain how those features were handled. This distinction matters because a numerical estimate can be clearly reported while the analysis needed to interpret it as a design-based treatment effect remains unclear.

The composite primary endpoint also illustrates a common trade-off. Combining related targets produces a single measure of joint control, which may be useful for a service model intended to integrate care. At the same time, the combined measure can conceal component-specific patterns and depends on exact rules for each component. The wording discrepancy in the blood pressure definition shows why operational clarity matters to reproducibility.

The record further illustrates why estimates, intervals, and p-values should be read together. The primary comparison has a positive-direction interval and an unadjusted p-value, while the secondary outcomes have different patterns and varying precision. Neither statistical significance nor a single endpoint can stand in for assessment of implementation, safety, missing data, or design assumptions.

For biostatisticians and clinical researchers, the central lesson is to separate what is numerically posted from what can be inferred about the study’s design and analysis. Transparent crossover methods, population accounting, multiplicity handling, and missing-data reporting would make this pilot’s findings more assessable and would support planning of subsequent evaluations.

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.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The registry record leaves important design and analysis details unresolved. Although the study is described as randomized and crossover, it does not specify the randomization unit, allocation method, or how the cluster sequences were analyzed. It does not report adjustment for cluster effects, period effects, sequence, or repeated measures, and it does not state whether the posted comparisons represent a model matched to the crossover design. The original sample-size justification is also not reported.

The primary outcome description contains an ambiguity: the initial blood pressure sentence uses “and/or,” while the dual-control definition uses “AND.” Since the endpoint requires a precise rule for classifying control, the record does not make clear which wording governed the reported percentage. The use of evidence of 6MMD for some missing viral-load results is noted, but the abbreviation and its implementation are not described further.

The primary outcome excludes eleven participants with incomplete data, but missingness by group, reason for missingness, and sensitivity analyses are not reported. The record does not explain every outcome-specific denominator or provide a complete account of the analysis populations. This limits assessment of selection and missing-data bias.

The record lists secondary outcomes for implementation and patient measures but does not report analyses for all of them. It does not provide a multiplicity strategy or a detailed statistical analysis plan. Safety reporting is also limited: serious-event terms are absent, and exposure time and event attribution during crossover periods are not explained. These are limitations of the available registry record; they should not be taken as proof that the study did not collect or analyze additional information outside the posted record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Task-shifted Adaptation of the WHO-PEN Intervention to Address Cardio-metabolic Complications in People Living With HIV in Zambia — NCT05005130.
• Registry record last updated 2024-01-30; status last verified 2023-11.
• Results first posted 2024-01-30.
• 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, unmasked crossover pilot of TASKPEN, an adapted task-shifted package of integrated HIV and noncommunicable disease services in Zambia. The primary endpoint was the change in the percent of participants with dual HIV and blood pressure control from baseline to 6 months. The posted percentages were 52.0% for standard of care and 60.0% for TASKPEN, with an unadjusted p-value of 0.008 and a risk-difference interval above zero.

The study also listed secondary outcomes concerning provider reach, HIV suppression, implementation characteristics, and cost. Serious adverse events affected zero participants in both reported groups; deaths and other adverse-event counts were also posted. Interpretation is limited by unreported crossover analysis details, incomplete-data handling, and multiplicity methods. The registry does not report the original sample-size justification or a detailed statistical analysis plan.