Multilevel HPV Self-Testing Intervention for the Increase of Cervical Cancer Screening Among Women in Appalachia: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Multilevel HPV Self-Testing Intervention for the Increase of Cervical Cancer Screening Among Women in Appalachia (NCT04411849), a randomized na study. The primary outcome is Effectiveness of Human Papillomavirus (HPV) Intervention.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. The record is marked completed, with an enrollment of 802. The listed intervention and usual-care arms have reported group sizes of 464 and 338, respectively. These are the group counts recorded in the results; the enrollment field and arm counts describe different registry entries and should not be treated as a substitute for information about participant flow.

The intervention combined mailed HPV self-test devices and cervical cancer information with telephone-based patient navigation for participants who did not return a self-test within a few weeks. Usual care consisted of a reminder letter to obtain clinic-based cervical cancer screening and cervical cancer information. The registry lists best practice, HPV self-collection, informational intervention, and a patient navigation program among the interventions.

The trial start date is 2021-08-27, and primary completion is recorded as 2024-06-11. The primary outcome timeframe is recorded as “Up to 1 years.” The record does not report further details about the duration of follow-up for individual participants, the timing of screening ascertainment, recruitment procedures, health systems involved, or allocation concealment. Masking is recorded as none.

The primary outcome description says the comparison would use generalized linear mixed models to account for correlation among women from the same health system. However, the registry reports zero analyses and does not provide a model-based result. The numerical comparison discussed in the posted results is therefore best read as the registry’s unadjusted group comparison, rather than as a reported result from the planned mixed model.

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 Effectiveness of Human Papillomavirus (HPV) Intervention, measured over Up to 1 years.

The primary endpoint is whether a participant was screened during the project. It is a binary, participant-level outcome: each participant is classified according to whether screening occurred. The results report counts of participants recorded as screened in each arm, alongside the arm sizes. The registry also describes the endpoint as the proportion of women screened.

This endpoint is relevant to the trial’s stated purpose because the intervention is intended to address cervical cancer screening, and the comparator also encourages screening through clinic-based care. Measuring whether screening occurred focuses on completion of the screening action, rather than on HPV test results, diagnosis, or later health outcomes. The registry record does not report those as primary outcomes.

The endpoint timeframe is recorded as “Up to 1 years.” The registry says the analysis was intended to use an intent-to-treat approach, meaning the planned comparison was based on assigned groups rather than a comparison limited to participants who used the self-test. The record does not describe how screening status was verified, how incomplete or unavailable outcome information was handled, or how the endpoint was defined for participants with uncertain screening status. Those details matter for understanding precisely what qualifies as screened and how every randomized participant contributes to the analysis.

7. Results Posted in the Registry

• Group I (Intervention): 14.9% (69/464) versus 5.0% (17/338) on control; risk difference 9.8 percentage points (95% CI 5.9 to 13.8), risk ratio 2.96 (1.77–4.93); unadjusted two-proportion z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

What does randomization contribute?

In general, random assignment creates groups that can be compared without choosing treatment based on participant characteristics. It supports an interpretation of group differences as associated with assignment, provided the trial is implemented and analyzed appropriately. Randomization does not guarantee that the groups are identical in every observed or unobserved characteristic, nor does it resolve problems from missing outcomes, departures from assigned care, or incomplete reporting. The registry records this trial as randomized, but the method used to generate the sequence and the approach to conceal allocation are not reported in the registry record.

What is the binary endpoint?

In general, a binary endpoint records whether an event or condition occurred for each participant. Here the event is being screened during the project. A count of participants with the event can be interpreted alongside the group size, and the resulting proportion describes how frequently the event was recorded within that group. Such an endpoint is direct and relatively easy to communicate, but its interpretation depends on a clear event definition and complete, comparable ascertainment in each group. Details about the screening verification process and missing endpoint records are not reported in the registry record.

What do the reported effect measures mean?

The risk difference is the contrast between the two group proportions, on the proportion scale. Its positive reported estimate indicates a higher recorded proportion in the intervention group. The risk ratio expresses the intervention-group proportion relative to the usual-care proportion. The odds ratio compares odds rather than proportions; when events are not rare, an odds ratio can differ materially from a risk ratio. These measures answer related but distinct questions. The risk difference is often useful for describing an absolute contrast, while ratios describe relative contrasts. The posted values are unadjusted and should not be interpreted as model-adjusted estimates.

A p-value is a measure of how compatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of a difference. The registry reports an unadjusted p-value of <0.001. The record does not provide a detailed account of the test used to obtain that p-value, beyond labeling the comparison unadjusted.

Why might a mixed model be planned?

The primary outcome description says generalized linear mixed models would be used to account for correlation among women from the same health system. In general, outcomes from people treated or observed within the same system may be correlated: they can share staff, procedures, access conditions, or other contextual influences. Treating every outcome as wholly independent can then misrepresent the uncertainty in a group comparison. A mixed model can represent this clustered structure, with model terms that account for within-system similarity while estimating the group contrast.

The registry record does not report the number of health systems, the model’s specific terms, the link function, the method used to estimate uncertainty, or a model-based result. It also does not report whether the posted unadjusted comparison accounts for clustering. The planned modeling approach is therefore useful context, but it cannot be used to reinterpret the posted effect estimates as adjusted findings.

What does intent-to-treat mean in this context?

In general, an intent-to-treat analysis compares participants according to their randomized assignment, regardless of whether they fully followed the assigned intervention. This preserves the comparison created by randomization and evaluates assignment to the intervention strategy, rather than only the experience of participants who completed every intervention step. The registry describes an intent-to-treat approach for the primary endpoint. It does not report how participants who never returned a self-test, crossed between care approaches, or lacked a recorded screening outcome were handled in the final analysis. Nor does the record provide participant-flow details that would show how the planned approach was implemented.

10. Confidence Intervals and Precision

The posted risk-difference estimate is 0.098, and its reported interval extends from 0.059 to 0.138. The reported intervals for the risk ratio and odds ratio are 1.772 to 4.933 and 1.902 to 5.721, respectively. The interval endpoints indicate a range of values compatible with the estimate under the method used to construct the interval. They communicate uncertainty around an estimated contrast rather than a range of individual participant outcomes.

In general, an interval is more informative than a point estimate alone because it shows how much uncertainty remains in the estimate. A narrower interval indicates greater precision for that particular quantity under the analysis assumptions; a wider interval indicates less precision. Interpretation also depends on the interval’s confidence level and calculation method. The confidence level and construction method are not reported in the registry record, so the intervals should be quoted as posted without assigning them a confidence level.

The intervals accompany the posted unadjusted comparison. They do not show whether the planned generalized linear mixed model would produce the same point estimate or uncertainty, and the registry reports no model-based analysis result. The intervals also do not account for unreported issues such as missing outcome information unless the underlying analysis method did so; that method is not described. Precision should therefore be considered alongside the analysis description and the gaps in reporting, rather than read as a complete account of uncertainty about the intervention strategy.

11. 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 values are participants per arm, not total event counts. They are illustrative calculations based on the observed effect, rather than a report of the assumptions used to design the trial. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial-design assumptions are not reported in the registry record.

For each assumed effect size, the 80% power column gives the illustrative number of participants per arm under those assumptions for an 80% chance of detecting that effect at the stated significance level, if the assumptions hold. The 90% power column gives the corresponding per-arm planning number for a 90% chance. These are prospective planning interpretations, not descriptions of what happened in the completed trial. This is not observed power.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For 100% of the observed effect, the figures are 145 participants per arm for 80% power and 193 for 90% power. For 75% of the observed effect, the figures are 229 and 305. For 50% of the observed effect, the figures are 449 and 600. The pattern illustrates a general planning principle: smaller effects are harder to detect and require more participants, all else equal. The calculations do not show that those effects are certain, or that the observed effect will recur in a future study. They also do not replace information about the original trial’s design rationale, which is not reported.

12. 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 = 0.050; treatment proportion p₁ = 0.149; average p̄ = 0.100.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4233 = 0.8297.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4176 = 0.3514.
4. n = (0.8297 + 0.3514)² / (0.0984)² = 144.0, rounded up to 145 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 <- 0.0502958579881657                          # control proportion
p1 <- 0.148706896551724                          # 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(4411849)
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 = 145 (80% power), 193 (90% power)
 75% of observed effect: n per arm = 229 (80% power), 305 (90% power)
 50% of observed effect: n per arm = 449 (80% power), 600 (90% power)
power.prop.test: 144 
Simulated power at n = 145 per arm: 0.819 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists one outcome measure and no secondary outcomes posted. It reports zero analyses. The primary outcome description states that the analysis would compare groups using generalized linear mixed models and an intent-to-treat approach, but the registry does not provide the planned model specification or a model-based result. It also does not report a detailed statistical analysis plan, including whether the primary comparison was designated before results were examined.

Multiplicity arises when several hypotheses, outcomes, groups, or analysis choices are tested. In general, evaluating many comparisons can increase the chance of finding an apparently unusual result by chance, and prespecified approaches may be used to address that issue. The registry record does not report a multiplicity adjustment or provide enough detail to determine what comparisons were planned beyond the primary outcome description. The absence of posted secondary outcomes does not establish whether other outcomes were collected or analyzed; such details are not reported in the registry record.

The registry describes an intent-to-treat analysis, but does not state how missing screening status was handled, whether any participants were excluded from the primary analysis, or how deviations from assigned care were treated. The record also does not report participant flow or the extent of missing outcome information. These omissions limit assessment of whether the posted comparison fully reflects the planned analysis population and how robust the result is to missing data.

For the same reason, it is not possible to determine from the registry record whether the unadjusted estimate was selected from multiple candidate analyses or whether the planned clustered model was fitted. The posted result should be read on its stated terms, with the unadjusted label and lack of model details kept in view. These are reporting limitations; they do not by themselves establish that a particular analysis choice was made.

14. 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.

The serious adverse event record lists zero affected participants in each arm and zero deaths. For other adverse events, the record also lists zero affected participants in each arm. The recorded groups at risk are 464 in the intervention arm and 338 in the usual-care arm. No serious adverse event terms are listed.

These entries describe what is reported in the registry’s adverse-event fields. They should not be read as proof that no adverse experiences occurred, or that the intervention has no safety risks. The registry record does not provide further definitions of the adverse-event categories, details of how events were collected, the observation period for safety reporting, or a narrative explaining the zero counts. It also does not report whether events were assessed as related to the intervention. The figures therefore summarize the recorded entries, while the completeness and scope of safety ascertainment remain unclear from the registry record.

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

The posted results show a higher recorded screening proportion in the intervention group than in the usual-care group, with a positive unadjusted risk difference of 0.098. The intervention group had 69 participants recorded as screened, compared with 17 in the usual-care group. The reported unadjusted p-value is <0.001, and the risk-difference interval runs from 0.059 to 0.138. Together, these values describe the observed group comparison and its reported statistical uncertainty.

They do not establish that the intervention will produce the same contrast in every health system or among all women in Appalachia. The registry does not report detailed eligibility criteria, recruitment methods, the number of health systems, or the results of the planned mixed model. Generalization depends on how closely other populations and care settings resemble the trial context, and the record does not provide enough detail to characterize that context fully.

The endpoint is screening during the project. It is not a measure of cervical cancer diagnoses, later health outcomes, or the accuracy of HPV self-testing. The posted results also do not separate the contribution of mailed devices, information, and telephone navigation; the intervention was described as a combined strategy. The results therefore cannot identify which component accounted for the observed group difference.

The registry’s zero adverse-event entries should be understood as recorded safety data, not as a guarantee of absence of harm. Missing details about event ascertainment and follow-up limit what can be concluded from those entries. Overall, the record supports a descriptive account of the posted screening comparison, while leaving important questions about analysis implementation, data completeness, and broader applicability unresolved.

16. Why This Trial Matters Statistically

This trial poses a statistical question about a practical screening outcome: whether participants were recorded as screened during the project. That outcome connects the intervention strategy to an observable behavior rather than only to knowledge or intention. The comparison also illustrates why the choice of effect measure matters. The risk difference describes the absolute contrast in proportions, while the risk ratio and odds ratio express relative contrasts on different scales.

The design combines randomization with an intervention that includes multiple components and planned follow-up for participants who do not return a self-test. Such a strategy makes the assigned-group comparison relevant to evaluating the combined approach. At the same time, a combined intervention does not identify the separate contribution of each component unless component-specific comparisons are built into the design and analysis; the registry does not report such comparisons.

The primary outcome description anticipates correlation among women from the same health system and names a generalized linear mixed model as the planned approach. This highlights an important design and analysis issue: observations within shared settings may not be independent. The registry’s posted comparison is unadjusted, however, and no mixed-model estimate is reported. Readers can therefore distinguish the planned statistical approach from the numerical result actually posted.

The record also demonstrates why an effect estimate should be read together with its interval, analysis label, and reporting context. The posted estimates are accompanied by intervals, but the confidence level and construction method are not specified. Missing details about participant flow, outcome ascertainment, and missing data further shape the limits of interpretation. These reporting features are part of the statistical meaning of the result, not merely administrative details.

17. 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.

Important trial-specific details are not reported in the registry record. The record does not give eligibility criteria, recruitment methods, participant characteristics, or the number and identities of the health systems involved. It is therefore difficult to assess how closely the enrolled group represents the wider population named in the trial title or how strongly the results might depend on local care settings.

Although randomization is recorded, the method used to generate the allocation sequence and the process for concealing allocation are not reported. Masking is recorded as none. The record does not describe how screening was verified, whether ascertainment was equivalent between groups, or how the timing of outcome measurement was applied to individual participants. It also does not provide a participant-flow account or explain missing screening outcomes.

The analysis description names an intent-to-treat approach and generalized linear mixed models to account for health-system correlation, but the registry reports zero analyses and does not present a model-based result. The posted comparison is unadjusted. The model specification, clustering details, and handling of missing data are not reported. The confidence level and construction method for the reported intervals are also not stated.

The intervention includes several components, so the group comparison does not isolate the effect of the self-test device, information, or navigation. Safety reporting lists zero affected participants for the recorded serious and other adverse-event categories, but event definitions, collection methods, and observation details are not reported. These limitations do not negate the posted results; they identify what the registry record leaves uncertain when assessing their precision, implementation, and applicability.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Multilevel HPV Self-Testing Intervention for the Increase of Cervical Cancer Screening Among Women in Appalachia — NCT04411849.
• Registry record last updated 2025-09-10; status last verified 2025-09.
• Results first posted 2024-12-04.
• 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.

21. Record Summary

NCT04411849 is a completed, randomized, unmasked, parallel-group trial of a multilevel HPV self-testing intervention for cervical cancer screening among women in Appalachia. The registry records enrollment of 802 and describes mailed self-test devices, cervical cancer information, and telephone-based navigation for participants who did not return a test, compared with usual care involving a reminder letter and information.

The primary endpoint was whether a participant was screened during the project, with an intent-to-treat approach and generalized linear mixed models described as planned. Posted results record 69 screened participants in the intervention group and 17 in usual care, with an unadjusted risk difference of 0.098 and p < 0.001. No model-based analysis result is reported. The adverse-event fields list zero affected participants in both groups. Details on missing outcomes, model implementation, and the confidence-interval method are not reported in the registry record.