Community Collaboration to Advance Racial/Ethnic Equity in CRC Screening: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Community Collaboration to Advance Racial/Ethnic Equity in CRC Screening (NCT05714644), a randomized na study. The primary outcome is CRC Screening Completion Rates.

2. Clinical Question

3. Trial Design

This was a completed, randomized, parallel-group clinical trial registered as NCT05714644. The registry describes the study as pragmatic and reports enrollment of 5127 participants. The setting was community health centers, and the population of interest was patients overdue for colorectal cancer screening.

Participants were assigned to one of two mailed outreach approaches: a FIT kit or a Cologuard test. Both tests were intended for at-home completion and return by mail. The listed allocation is randomized, the model is parallel, and the masking designation is single. Who was masked, and how masking was maintained, are not reported in the registry record. The trial phase is listed as NA.

The primary outcome was completion of the stool-based screening test within 3 months. The registry also lists screening completion at 6 months and diagnostic colonoscopy completion at 6 months. Enrollment was 5127; the posted outcome denominators are 2435 for the mailed FIT group and 2692 for the Cologuard group on the primary outcome. The record does not explain the relationship between overall enrollment and these outcome denominators.

The study started on 2023-06-07, had primary completion on 2024-06-30, and is marked completed. The sponsor is Massachusetts General Hospital. Further details about recruitment, allocation procedures, implementation across centers, or the original statistical design 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.

Before assignment: No enrolled patients were excluded from the study before assignment to arms.

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 CRC Screening Completion Rates, measured over 3 months.

The primary endpoint is the count of participants who completed the stool-based screening test assigned to them, assessed within 3 months. Completion means completing the FIT or Cologuard test; the registry describes the endpoint as completion of the stool-based screening test. The endpoint is binary at the participant level: each participant either completed the assigned test or did not.

Completion is directly relevant to the outreach comparison because mailing a test can only lead to screening if the recipient completes and returns it. A count alone does not account for how many participants were assigned to each group, so it is interpreted alongside each group’s denominator and as a comparison of completion proportions. The posted counts are 550 of 2435 in the mailed FIT group and 751 of 2692 in the Cologuard group.

This endpoint measures completion of the mailed screening test, not detection of cancer, diagnostic accuracy, or subsequent health outcomes. The registry’s secondary outcomes extend the assessment to completion at 6 months and diagnostic colonoscopy completion at 6 months. The primary endpoint’s timeframe and definition make it a measure of screening uptake over the specified follow-up period, rather than a measure of longer-term clinical benefit.

7. Results Posted in the Registry

• Cologuard: 27.9% (751/2692) versus 22.6% (550/2435) on control; risk difference 5.3 percentage points (95% CI 2.9 to 7.7), risk ratio 1.24 (1.12–1.36); unadjusted two-proportion z-test p = <0.001.

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.

CRC Screening Completion Rates

• 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:
  • Cologuard: 31.7% (854/2692) versus 26.7% (649/2435) on control; risk difference 5.1 percentage points (95% CI 2.6 to 7.6), risk ratio 1.19 (1.09–1.30); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Cologuard than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Diagnostic Colonoscopy Completion Rates

• 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:
  • Cologuard: 39.7% (23/58) versus 31.0% (13/42) on control; risk difference 8.7 percentage points (95% CI -10.1 to 27.5), risk ratio 1.28 (0.74–2.23); unadjusted two-proportion z-test p = 0.371.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Cologuard and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary question in two directions: whether screening-test completion remains different when assessed at 6 months, and whether diagnostic colonoscopy is completed. The posted unadjusted comparisons suggest a consistent direction for screening-test completion across the primary and later assessment, while the colonoscopy comparison is much less precise. This overall pattern is compatible with more screening-test completion in the Cologuard group, but it does not make the secondary outcomes confirmatory evidence for the primary result.

The endpoints represent different steps in the screening process. Completion of a mailed stool-based test is not the same outcome as completion of a diagnostic colonoscopy. The colonoscopy endpoint concerns participants reported in the relevant outcome groups and does not measure screening completion for all randomized participants. The registry does not describe the pathway or eligibility rules leading to the colonoscopy denominator, so the relationship between screening-test completion and this secondary outcome cannot be fully assessed.

Secondary findings generally carry less inferential weight when many outcomes or comparisons are considered, especially if no adjustment or prespecified testing sequence is reported. Testing multiple hypotheses increases the chance that at least one result appears notable by chance. The registry does not report a multiplicity strategy, so the degree to which the secondary analyses were planned or adjusted is unknown. The 6-month screening outcome also concerns a later assessment of the same general behavior as the primary endpoint, rather than an entirely independent confirmation.

The registry posts a sponsor analysis for the 6-month screening-completion outcome but no sponsor analysis for diagnostic colonoscopy completion. The distinction between sponsor-reported and unadjusted results should therefore be retained across endpoints. The secondary results provide context about the pattern of recorded outcomes, but they do not replace the primary comparison or establish broader clinical effects.

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

• CRC Screening Completion Rates
• Diagnostic Colonoscopy Completion Rates

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because each participant either completed the assigned screening test within the specified timeframe or did not. For a binary outcome, a risk is the proportion of participants with the event in a group. The risk difference subtracts one group’s risk from the other group’s risk. Here the comparison is Cologuard relative to mailed FIT, so a positive risk difference indicates greater completion in the Cologuard group. The registry’s sponsor analysis reports a risk difference, while the separate recalculation uses the posted counts and denominators without adjustment.

What does the regression result represent?

The sponsor’s method is listed as logistic regression, with the reported parameter described as risk difference. Logistic regression models the probability of a binary outcome using a log-odds scale; a risk difference expresses the contrast on the probability scale. The registry does not describe the model specification, covariates, handling of center-level structure, or the procedure used to obtain the reported risk difference from the regression. It is therefore not possible to determine from the record exactly how the adjustment was performed or what variables were included.

The recalculated comparison is unadjusted: it uses the posted group counts and denominators only. It does not incorporate covariates or other design features. An unadjusted estimate can differ from an adjusted estimate when the analysis methods or information used differ. The registry does not give enough detail to identify why the sponsor result and recalculation differ. Given the recorded discrepancy, the sponsor’s own analysis takes precedence as the trial’s reported analysis; the recalculation remains a descriptive, unadjusted check based on the posted summaries.

How should the p-value and interval be read?

A p-value evaluates how compatible the observed data are with a specified null hypothesis under the analysis model. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of an effect. A confidence interval gives a range of estimates compatible with the data and model at the stated confidence level. It communicates uncertainty about the estimated difference, rather than a range containing a fixed proportion of individual participant outcomes.

The sponsor reports a 95% confidence interval and p = 0.05 for the primary comparison. The unadjusted recalculation reports p < 0.001. These values arise from different analyses and should not be blended or treated as interchangeable. The sponsor’s result is the reported inferential analysis, whereas the recalculated result is unadjusted. The registry does not report whether the sponsor used any prespecified threshold or decision rule beyond the information in the posted analysis.

Why can over-dispersion matter?

Over-dispersion describes variability in data that exceeds what a model assumes. It is particularly relevant for some count outcomes, where a simple model may expect variance to follow a specified relationship with the mean. The registry reports participant counts for binary completion outcomes, rather than a rate or count process with a stated dispersion parameter. No dispersion estimate is posted for these endpoints, and the listed outcome type does not establish that an over-dispersion adjustment was needed. More generally, if observations are more variable or more dependent than a model assumes, standard errors and confidence intervals can be too narrow unless the analysis accounts for that structure.

Other analysis details that would help assess the methods are not reported in the registry record. These include the original statistical analysis plan, the prespecified covariates, treatment of missing outcomes, analysis population, handling of participants across multiple centers, and whether any interim analyses occurred. Their absence does not establish that these procedures were not conducted; it means the registry record does not document them.

11. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimated difference. The sponsor’s primary analysis reports a 95% confidence interval from 0.8 to 8.7 for the risk difference. The unadjusted recalculation reports a 95% confidence interval from 0.029 to 0.077. These intervals are on differently presented scales in the registry outputs, and they belong to different analyses. The sponsor interval should be used when describing the sponsor’s reported analysis; the recalculated interval describes the unadjusted estimate.

A confidence interval is not a guarantee that the true effect lies within its endpoints. Rather, it expresses the range of values reasonably compatible with the data and the method under repeated use of that method. A narrower interval indicates greater precision than a wider interval, but interval width also depends on the analysis and assumptions. Precision does not determine clinical importance by itself.

The sponsor’s interval is entirely above zero, indicating that its reported estimates are positive under the stated analysis. The unadjusted interval is also above zero. However, the discrepancy between the two analyses matters: the sponsor result is the trial’s reported analysis, and the unadjusted recalculation should not replace it. The registry does not explain the discrepancy or provide enough model detail to assess its source.

The diagnostic-colonoscopy comparison has a 95% unadjusted interval from -0.101 to 0.275, spanning zero. This interval is broad relative to its estimate and indicates substantial uncertainty. Its interpretation also differs from the primary outcome because it concerns a smaller posted denominator and is a secondary endpoint. Confidence intervals help make these differences in precision visible; they do not by themselves resolve questions about multiplicity, missing data, or generalizability.

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 estimates are participants per arm, not total participants and not total events. They are illustrative calculations based on the observed effect, rather than the trial’s original design assumptions. The registry describes the calculation assumptions as a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is a stated fraction of the observed effect. The original trial design assumptions, including its sample-size justification, are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a future study to have an 80% chance of detecting the selected effect under the stated assumptions, if that effect is real and the assumptions hold. The 90% power column gives the corresponding planning estimate for a 90% chance. These are design probabilities, not probabilities that a result is true. For the primary endpoint, planning for 100% of the observed effect corresponds to 1,050 participants per arm for 80% power and 1,405 for 90% power. Planning for 75% of the observed effect corresponds to 1,834 and 2,454 participants per arm, respectively. Planning for 50% of the observed effect corresponds to 4,051 and 5,423 participants per arm.

Smaller effects are harder to distinguish from random variation, so the estimates require more participants per arm when the target effect is reduced. The curve should be read as a visual expression of that relationship, not as a new trial result. These calculations are not observed power; they are planning illustrations based on the observed effect, and they do not establish what the original study was designed to detect.

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 = 0.226; treatment proportion p₁ = 0.279; average p̄ = 0.252.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6143 = 1.2041.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6132 = 0.5161.
4. n = (1.2041 + 0.5161)² / (0.0531)² = 1,049.3, rounded up to 1,050 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 <- 0.225872689938398                          # control proportion
p1 <- 0.278974739970282                          # 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(5714644)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,050 (80% power), 1,405 (90% power)
 75% of observed effect: n per arm = 1,834 (80% power), 2,454 (90% power)
 50% of observed effect: n per arm = 4,051 (80% power), 5,423 (90% power)
power.prop.test: 1049.3 
Simulated power at n = 1,050 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. Analyses Reported by the Sponsor

The sponsor’s primary analysis is reported as logistic regression with the parameter expressed as a risk difference. It gives a risk difference of 4.7, a 95% confidence interval from 0.8 to 8.7, and p = 0.05. The separate unadjusted recalculation from the posted counts gives a risk difference of 0.053, a 95% confidence interval from 0.029 to 0.077, and p < 0.001.

These are not identical estimates or inferential results. The registry marks a discrepancy, but does not explain its source. The recalculation is based on the posted summary counts and is unadjusted; the sponsor’s analysis is the trial’s own reported analysis. Accordingly, the sponsor’s analysis takes precedence when describing the reported trial result. The recalculation can help readers understand the simple comparison of the posted group summaries, but it should not be presented as a correction or replacement for the sponsor’s analysis.

The registry does not provide enough information to reproduce the regression analysis or determine why it differs from the unadjusted result. Details such as model covariates and the exact computation of the risk difference are not reported in the registry record. Interpretation should retain that uncertainty rather than infer a cause.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary screening-completion endpoint and secondary outcomes for screening completion and diagnostic colonoscopy completion. It does not report how the investigators handled multiplicity, such as whether a hierarchy of hypotheses, adjustment of significance levels, or another prespecified approach was used. Without that information, the chance of false-positive findings across multiple tests cannot be evaluated from the registry record.

Missing outcome information is also not described in enough detail to assess its possible effect. The registry provides group denominators for the posted outcomes, but does not state how missing or unreturned tests were classified, whether follow-up differed between groups, or whether any imputation or sensitivity analyses were performed. The primary outcome is defined as test completion, but additional rules for handling unavailable status are not reported in the registry record.

The analysis population is not specified. The record does not say whether the analyses followed an intention-to-treat approach, included only participants with available outcome data, or used another population definition. It also does not describe exclusions after randomization or how participants were handled if their assigned test was not completed.

The original statistical analysis plan, any interim analyses, and the original sample-size justification are not reported in the registry record. These omissions limit assessment of whether the posted analyses match prespecified methods and whether the study was planned around a particular target effect. They do not establish that procedures were absent; they indicate that the registry record does not document them. As a result, the primary result can be described using the posted sponsor analysis, but the full safeguards around outcome selection, missing data, and multiple testing cannot be verified from the record.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry reports zero serious adverse events, zero other adverse events, and zero deaths in both groups. The figures are reported for 2435 participants in the mailed FIT group and 2692 in the Cologuard group. No serious adverse event terms are listed.

These figures describe what was recorded in the registry for the reported groups. They do not establish that no adverse events occurred outside the registry’s reporting definitions or observation process. The record does not provide additional detail about how adverse events were collected, the period of safety follow-up, attribution to the screening approach, or completeness of reporting.

The trial’s central comparison concerns completion of mailed screening tests. The safety counts should be interpreted separately from that effectiveness-related endpoint: they do not measure screening completion and do not explain the difference in completion results. Zero recorded events in these fields should be reported as registry counts, not as proof of absence of risk.

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

The posted primary results describe completion of mailed colorectal cancer screening tests in a randomized comparison conducted in community health centers among patients overdue for screening. The sponsor’s reported regression analysis estimates a positive risk difference favoring the Cologuard group for completion within 3 months. The unadjusted recalculation from posted counts is also positive, but differs from the sponsor estimate and has a different p-value. Because the registry records a discrepancy, the sponsor’s analysis takes precedence as the trial’s reported inferential result.

The outcome is uptake of the mailed test, not cancer detection, diagnostic accuracy, treatment, or health benefit. A difference in completion does not by itself establish which test is more feasible or acceptable, even though those were questions identified in the trial description. Those measures are not reported in the registry record. Nor do the completion results establish whether participants received appropriate follow-up or experienced different health outcomes.

The secondary pattern offers context but has limitations. Screening completion at 6 months follows the same broad direction in the unadjusted comparison, whereas diagnostic-colonoscopy completion is uncertain. These secondary findings should be treated cautiously because a multiplicity strategy is not reported and no sponsor analysis is posted for the colonoscopy endpoint.

The findings apply most directly to the study’s described setting and population. The registry does not provide enough demographic, implementation, or analysis detail to determine how results might vary across different communities or service settings. The posted results therefore support a statistical description of completion in this trial, not a universal claim about screening programs or a recommendation for individual care.

18. Why This Trial Matters Statistically

This trial raises a practical statistical question about how the design of mailed outreach relates to completion of a screening test. Random allocation creates a basis for comparing the two approaches, while a participant-level binary endpoint makes the outcome directly interpretable as completed or not completed. Reporting group counts alongside denominators helps distinguish the number of completions from the proportion of participants who completed testing.

The primary result also illustrates why the estimand and analysis method matter. The sponsor reports a regression-based risk difference, while a simple unadjusted recalculation from the posted summaries produces a different estimate and p-value. Readers need to know which result is the trial’s own analysis and which is a summary-based recalculation. The registry’s discrepancy flag makes this distinction especially important, and the lack of model details limits independent assessment of the sponsor estimate.

Precision and endpoint hierarchy matter as well. The primary completion outcome and later secondary outcomes answer related but distinct questions. Screening-test completion, diagnostic colonoscopy completion, and clinical benefit are not interchangeable. Confidence intervals indicate how uncertain the estimated comparisons are, while the secondary status and lack of a reported multiplicity strategy constrain how strongly secondary findings can be interpreted.

Finally, the planning illustrations show how sample-size requirements depend on the effect a future study aims to detect. They are not evidence about the original trial’s design rationale. Together, these features make the record useful for teaching the difference between a posted event count, a risk difference, a sponsor-reported model, and an unadjusted recalculation—and for recognizing which unanswered analysis details limit interpretation.

19. Limitations

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

Several limitations specific to this record constrain interpretation. The registry does not report participant characteristics, eligibility details beyond being overdue for screening, or outcome results by community health center. It is therefore not possible to assess whether completion differed across population subgroups or centers, or how broadly the results may apply.

The primary endpoint is test completion, not the accuracy or clinical consequences of screening. The registry identifies feasibility and acceptability as questions of interest but does not post measures for them. It also does not explain how diagnostic colonoscopy participants were selected or how the colonoscopy outcome relates to the earlier screening outcome.

The sponsor’s primary analysis and the unadjusted recalculation differ, and the registry does not explain why. Model details, covariate adjustment, the analysis population, handling of missing outcomes, and any sensitivity analyses are not reported in the registry record. These gaps prevent independent reproduction of the sponsor analysis and make it difficult to assess the robustness of the result.

Multiplicity procedures and the original sample-size justification are also not reported. The planning illustrations use the observed effect and should not be mistaken for the study’s design rationale. The registry does not describe masking beyond the single-masking designation, including who was masked. Finally, the safety fields report no events but do not provide detailed collection or follow-up methods. These limitations concern the available record and do not establish that the underlying study lacked procedures or data not posted there.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Community Collaboration to Advance Racial/Ethnic Equity in CRC Screening — NCT05714644.
• Registry record last updated 2025-12-26; status last verified 2025-12.
• Results first posted 2025-12-26.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT05714644 is a completed randomized, parallel-group trial sponsored by Massachusetts General Hospital. It compared mailed FIT kits with mailed Cologuard tests among patients overdue for colorectal cancer screening in community health centers. Enrollment was 5127, and the primary endpoint was stool-based test completion within 3 months.

The sponsor reports a regression-based risk difference of 4.7, with a 95% confidence interval from 0.8 to 8.7 and p = 0.05. An unadjusted recalculation from the posted counts differs; the registry marks a discrepancy, so the sponsor’s own analysis takes precedence. Secondary outcomes cover screening completion and diagnostic colonoscopy completion at 6 months. The registry does not report the original statistical plan, missing-data procedures, multiplicity approach, or detailed model specification.