Health Literacy Interventions to Overcome Disparities in CRC Screening: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Health Literacy Interventions to Overcome Disparities in CRC Screening (NCT02360605), a randomized na study. The primary outcome is Initial CRC Screening.

2. Clinical Question

The broader study aims included comparing the follow-up approaches for initial and repeat screening, comparing their cost effectiveness, evaluating implementation and barriers, and exploring whether effects varied by literacy skills. The posted primary result addresses initial screening, not all of those aims. The registry record does not report a posted result for repeat screening or cost effectiveness, and it does not report secondary outcome results. The comparison is between two follow-up strategies layered onto the described education and demonstration, rather than a comparison of education with no education.

3. Trial Design

This was a randomized, parallel-group trial with no masking. The registry lists an enrollment of 620 and describes two behavioral follow-up approaches: an automated telephone reminder and a prevention coordinator. Both arms included health-literacy-appropriate education and a demonstration of FIT kits with simplified instructions. The difference described between the arms was how reminders to complete FIT screening were delivered.

The registry record lists the trial as completed, with a start date of 2015-02 and primary completion on 2018-11-06. The phase is listed as NA. The primary outcome was initial CRC screening, recorded as a count of participants. Its stated timeframe was 6 months after receipt of the FIT kit, and its description defined a participant as initially screened if a FIT was completed within 6 months of study entry. The record does not clarify any distinction between those two timing descriptions.

For the posted primary outcome, the automated telephone reminder arm included 308 participants and recorded 213 screened participants. The prevention coordinator arm included 306 participants and recorded 205 screened participants. The registry lists 3 outcome measures and 3 analyses, but no secondary results are posted. The analysis populations, allocation procedures beyond randomization, and details of any stratification or concealment 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

Reasons for not completing this period:

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: 6 patients withdrew within a day of enrolling and therefore were not included in the CRC analysis

6. Primary Endpoint

The registry lists the primary outcome as Initial CRC Screening, measured over 6 months after receipt of FIT kit.

The primary endpoint is initial colorectal cancer screening, measured as the number of participants who completed a fecal immunochemical test. The registry defines a participant as screened if a FIT was completed within 6 months of study entry; the listed timeframe says 6 months after receipt of the FIT kit. These descriptions identify a six-month assessment window, although the exact timing anchor is not clarified further in the registry record.

A binary outcome is appropriate for this endpoint because each participant is classified according to whether screening was completed within the specified period. The posted arm counts are 213 of 308 in the automated telephone reminder arm and 205 of 306 in the prevention coordinator arm. Such counts allow comparison of the proportion completing screening while retaining the number of participants in each arm as the denominator. The primary endpoint captures initial screening completion, not whether screening was repeated annually, the quality of the test, or later clinical outcomes.

FIT screening completion is used as a behavioral outcome relevant to the study’s stated goal of promoting CRC screening. It does not by itself measure the effectiveness of a screening test, detect cancer, or establish the effect of either follow-up strategy on health outcomes. The registry record does not report the primary endpoint’s handling of participants with missing screening status.

7. Results Posted in the Registry

• Prevention Coordinator Arm: 67.0% (205/306) versus 69.2% (213/308) on control; risk difference -2.2 percentage points (95% CI -9.5 to 5.2), risk ratio 0.97 (0.87–1.08); unadjusted two-proportion z-test p = 0.565.

8. Statistical Interpretation

9. Statistical Methods Explained

What is the endpoint’s data type?

The outcome is binary at the participant level: a participant either completed a FIT within the stated initial-screening window or did not. The registry presents the outcome as counts of participants. A comparison of binary outcomes can be expressed using absolute differences in proportions or relative measures such as risk ratios and odds ratios. These measures describe the same underlying arm comparison in different ways, so their numerical scales are not interchangeable.

A risk difference expresses the absolute contrast between the two arm proportions. A negative value in this comparison corresponds to a lower proportion in the prevention-coordinator arm than in the automated telephone reminder arm. A risk ratio compares the proportions as a ratio, while an odds ratio compares the odds of screening. The recalculated estimates are unadjusted comparisons derived from the posted summary counts. They do not account for participant-level covariates or other model features.

What does the reported analysis tell us?

The registry reports a mixed models analysis and a p-value of 0.61 for the comparison. A mixed model is a broad class of models that can represent outcomes while accounting for grouping or repeated observations, depending on how the model is specified. The registry record does not report the model details, the terms included, or the reason this method was selected. It is therefore not possible to identify which features the reported model addressed from the registry entry alone.

A p-value describes how compatible the observed data are with a specified null hypothesis 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 an effect. The registry’s p-value should be read together with the observed counts and, where available, effect estimates and confidence intervals. The reported sponsor analysis does not include an estimate or confidence interval in the posted results.

What is the role of the recalculation?

The unadjusted recalculation uses the posted arm counts and participant numbers to compare the observed proportions. It gives a risk-difference estimate, confidence interval, and p-value of 0.565, as well as relative measures. This is a simple comparison of summary statistics, not a reproduction of the mixed models analysis. Because the recalculation is unadjusted, it may differ from a model-based analysis that uses additional information or assumptions. The registry marks no discrepancy between the posted result and recalculation, but the analyses remain distinct in method.

Confidence intervals describe a range of effect values compatible with the data and the interval procedure. For the risk difference, zero represents no absolute difference. For a risk ratio or odds ratio, one represents no relative difference. The recalculated intervals include these no-difference values, which is consistent with the p-values not providing evidence of a statistically detectable between-arm difference at the stated planning threshold. The intervals also extend to effects in either direction, so uncertainty about the direction and size remains.

Why can over-dispersion matter?

For count outcomes, over-dispersion means that variability is greater than expected under a model’s assumed distribution. When a model understates variability, standard errors can be too small and confidence intervals too narrow. A binary participant outcome is not automatically subject to the same count-model issue; appropriate modeling depends on the data structure and the chosen model. The registry describes this outcome as participant counts and names a mixed models analysis, but it does not report a dispersion assessment or details that would establish whether over-dispersion was relevant.

What statistical details remain unknown?

The registry record does not report whether the primary analysis followed intention-to-treat principles, whether all randomized participants were included, how missing outcomes were handled, or whether any participants were excluded from analysis. It also does not report covariate adjustments, model diagnostics, or a detailed statistical analysis plan. Randomization is listed, but the record does not state how the random sequence was generated or concealed. These details matter when judging how closely the analysis corresponds to the original assignment and how robust the estimate may be to incomplete outcome data or model assumptions.

10. Confidence Intervals and Precision

Precision concerns the range of effect estimates compatible with the observed data under the interval method. The unadjusted risk-difference interval extends from a negative value to a positive value, crossing zero. It therefore permits both a lower screening proportion with prevention-coordinator follow-up and a higher proportion with that approach, as well as no absolute difference. The recalculated relative-risk and odds-ratio intervals also cross their respective no-difference values. The sponsor’s reported mixed models result does not include a confidence interval in the registry record.

Crossing a no-difference value does not show that the true effect is exactly zero. It means the observed data do not sharply distinguish the no-difference possibility from effects on either side under the method used. The intervals should not be read as probabilities that a particular effect is true. Rather, they convey uncertainty about the estimated contrast and its magnitude.

The arm counts are similar in size, but the registry’s outcome information does not remove uncertainty about the comparison. The available intervals leave room for meaningful differences in either direction; the record does not define a threshold for a clinically or operationally important difference. Consequently, statistical uncertainty cannot be translated into a conclusion about practical equivalence.

The recalculated intervals are based on an unadjusted comparison of posted summary statistics. Their precision and interpretation may differ from intervals produced by the sponsor’s mixed models analysis. Since the sponsor analysis interval is not reported, direct comparison of precision between the two methods is not possible. The posted data support a cautious reading: the direction and size of any underlying difference remain uncertain.

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 figures are participants per arm, not total events. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to a stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

For planning at 100% of the observed effect, the illustration gives 7,295 participants per arm for 80% power and 9,766 participants per arm for 90% power. For planning at 75% of the observed effect, it gives 12,912 participants per arm for 80% power and 17,284 participants per arm for 90% power. For planning at 50% of the observed effect, it gives 28,918 participants per arm for 80% power and 38,712 participants per arm for 90% power.

In plain terms, the 80% power column describes the planned number per arm under which the assumed effect would be detected in 80% of repeated studies if the planning assumptions and effect were correct. The 90% column uses a higher target probability of detection, which requires more participants under these assumptions. A smaller effect is harder to distinguish from random variation, so planning for a smaller fraction of the observed effect requires more participants per arm. These are planning illustrations based on the observed effect, not observed power and not a retrospective assessment of the trial’s success.

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 = 0.692; treatment proportion p₁ = 0.670; average p̄ = 0.681.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6593 = 1.2922.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6591 = 0.5547.
4. n = (1.2922 + 0.5547)² / (-0.0216)² = 7,295.0, rounded up to 7,295 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 <- 0.691558441558442                          # control proportion
p1 <- 0.669934640522876                          # 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(2360605)
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 = 7,295 (80% power), 9,766 (90% power)
 75% of observed effect: n per arm = 12,912 (80% power), 17,284 (90% power)
 50% of observed effect: n per arm = 28,918 (80% power), 38,712 (90% power)
power.prop.test: 7295 
Simulated power at n = 7,295 per arm: 0.797 (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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison as a mixed models analysis with p = 0.61. It does not report the corresponding effect estimate or confidence interval. The separate unadjusted recalculation from posted arm summaries gives p = 0.565 and includes effect estimates and intervals. These are not identical analyses: the recalculation compares summary proportions without the model specification used by the sponsor.

The registry marks no discrepancy between the reported result and the recalculation. The recalculated result can help readers understand the raw arm comparison, but it should not be presented as though it reproduces the mixed models analysis. The sponsor result remains the reported analysis of record, while the recalculation is a supplementary, unadjusted check based on the posted summaries.

Both p-values are above the 0.05 significance level used in the planning illustration, and neither provides clear statistical evidence of a between-arm difference in initial screening. That does not establish equivalence, and the absence of a sponsor confidence interval limits assessment of the model-based estimate’s precision. Further details about the model and its analysis population are not reported in the registry record.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists 3 outcome measures and 3 analyses, while no secondary results are posted. The study description includes several aims: initial and repeat screening, cost effectiveness, process evaluation, variation in effects by literacy skills, and exploration of patient characteristics related to screening knowledge, beliefs, self-efficacy, and compliance over time. The posted primary outcome result addresses initial screening. The record does not show results for the other stated aims.

When a study evaluates multiple outcomes, comparisons, or subgroups, the chance of at least one apparently notable result can increase. Statistical approaches may address multiplicity by adjusting inference or by distinguishing primary from exploratory analyses. The registry record does not report a multiplicity strategy, an order of testing, or which analyses were prespecified beyond identifying the primary outcome. It is therefore not possible to determine how the reported p-value should be interpreted in relation to all planned comparisons.

The record also does not report the analysis population or whether participants were analyzed according to randomized assignment. Although outcome counts and arm denominators are posted, the registry does not describe the handling of missing screening status, withdrawals, exclusions, or incomplete follow-up. It does not report imputation procedures or sensitivity analyses for missing data. The number of participants with unavailable outcome information, if any, is not reported in the registry record.

These omissions limit assessment of whether the analyzed participants represent the randomized groups and whether missing outcomes could affect the comparison. They also prevent a full evaluation of the model-based analysis and the relationship between the primary result and other planned analyses. No additional analysis details should be inferred from the counts or the mixed models label 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.

The registry lists serious adverse events in 0 of 308 participants in the automated telephone reminder arm and 0 of 306 participants in the prevention coordinator arm. It also lists other adverse events in 0 of 308 and 0 of 306, respectively. The adverse-event entry therefore records no serious or other adverse events in either arm during the reported accounting.

The registry separately lists 0 deaths in the automated telephone reminder arm and 1 death in the prevention coordinator arm. The record does not report the timing, cause, or relationship of that death to study participation or an intervention. The death count should not be interpreted as an intervention-related event without that information.

These figures describe what is posted in the registry record, not a complete characterization of safety. Event definitions, collection procedures, follow-up duration for safety, and attribution methods are not reported in the registry record. Counts of zero mean no events were recorded in the posted categories; they do not by themselves establish that no events occurred outside the registry’s reporting scope.

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

The primary result describes initial FIT completion in two randomized groups that both received health-literacy-appropriate education, a kit demonstration, and simplified instructions, but differed in reminder delivery. The posted counts were 213 of 308 in the automated telephone reminder arm and 205 of 306 in the prevention coordinator arm. The sponsor’s mixed models analysis reports p = 0.61, while the unadjusted recalculation reports p = 0.565. The recalculated confidence intervals include no difference and allow effects in either direction.

These findings do not establish that prevention-coordinator reminders are better or worse than automated telephone reminders. They also do not demonstrate that the approaches are equivalent, since the registry does not report an equivalence margin and the uncertainty intervals include differences in both directions. The primary result is compatible with uncertainty about the size and direction of the contrast.

The comparison does not measure either reminder strategy against no reminder or no education. It therefore cannot isolate the effect of the shared education and demonstration from the effect of follow-up. It also does not answer whether either approach improved repeat screening, altered cost effectiveness, reduced implementation barriers, or had different effects by literacy level. Those results are not reported in the registry record.

The endpoint is completion of initial screening within the stated timeframe, not cancer detection, diagnosis, later treatment, or health outcomes. The registry record also leaves the exact timing anchor somewhat unclear by describing the endpoint as within 6 months of study entry while listing the timeframe as 6 months after receipt of the FIT kit. Interpretation should remain focused on the outcome and analysis actually posted, rather than extending the result to outcomes or comparisons not reported.

17. Why This Trial Matters Statistically

This trial presents a useful statistical comparison of two ways to deliver follow-up after shared health-literacy-appropriate education and FIT demonstration. That distinction matters: the primary contrast is between a human prevention coordinator and an automated telephone reminder, not between screening support and no support. The design targets an implementation question about how follow-up is delivered.

The result also illustrates why participant counts, effect estimates, confidence intervals, and model-based analyses should be read together. The arm counts are close in size, but counts alone do not express the proportion screened. The unadjusted recalculation provides a risk-difference comparison and interval, while the sponsor reports a mixed models p-value without a corresponding estimate or interval. Neither analysis gives clear evidence of a between-arm difference, and the intervals preserve uncertainty about direction and magnitude.

Planning for effects smaller than the observed effect leads to substantially larger required per-arm sample sizes under the stated assumptions. This reinforces that detecting modest contrasts can require many participants, even when an observed comparison is available for planning. The figures are planning illustrations rather than evidence about the trial’s observed power or the rationale for its original enrollment.

Finally, the registry record distinguishes the primary initial-screening result from broader aims that include repeat screening, costs, process evaluation, and literacy-related differences. Keeping those questions separate prevents a narrow primary outcome from being treated as a complete answer to the larger research program.

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.

The registry record does not report detailed eligibility criteria, participant characteristics, or the analysis population for the primary outcome. It describes the intended focus on low-income patients, but the posted information does not show how representative the enrolled participants were or which participants contributed to the primary analysis. The listed enrollment is 620, while the outcome counts are reported for the two arms; the record does not explain any difference between the enrollment figure and the analysis denominators.

The endpoint timing is described both as screening within 6 months of study entry and as an assessment 6 months after receipt of the FIT kit. The record does not clarify whether these timing descriptions refer to the same anchor. It also does not report missing outcome counts, loss to follow-up, or the handling of incomplete screening information.

The sponsor’s mixed models result is reported with a p-value but without an effect estimate or confidence interval, and the model specification is not described. The unadjusted recalculation is based on arm summaries and cannot supply missing details about the sponsor’s model. Randomization is listed, but sequence generation, concealment, any stratification, and the analysis approach to randomized assignment are not reported.

Although the study description lists broader aims, secondary results are not posted. Multiplicity handling and the prespecification of secondary or exploratory comparisons are also not reported. Safety reporting gives event counts but does not describe event definitions, duration of safety follow-up, attribution, or the circumstances of the death listed in the prevention coordinator arm. These reporting gaps constrain interpretation of both the efficacy comparison and the safety information.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Health Literacy Interventions to Overcome Disparities in CRC Screening — NCT02360605.
• Registry record last updated 2021-06-30; status last verified 2021-06.
• Results first posted 2021-06-23.
• 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 record describes a completed randomized, parallel-group trial with no masking and an enrollment of 620. It compared automated telephone reminders with prevention-coordinator reminders after health-literacy-appropriate education and FIT demonstration. The primary outcome was initial CRC screening, defined by FIT completion within the stated six-month window.

The posted primary counts were 213 of 308 participants in the automated telephone reminder arm and 205 of 306 in the prevention coordinator arm. The sponsor reported a mixed models p-value of 0.61; an unadjusted recalculation reported p = 0.565, with confidence intervals that include no difference. No secondary results are posted. The registry lists no serious or other adverse events in either arm and 1 death in the prevention coordinator arm, without further details about that death.