Assessing the Effect of a Blood-based Colorectal Cancer Screening Test on Screening Adherence and Colonoscopy Completion: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Assessing the Effect of a Blood-based Colorectal Cancer Screening Test on Screening Adherence and Colonoscopy Completion (NCT03598166), a randomized na study. The primary outcome is Percentage of Participants Who Undergo Screening Within 6 Months of Outreach.

2. Clinical Question

The trial asked whether offering a blood-based colorectal cancer screening test as part of outreach was associated with more screening completion among patients who had declined both colonoscopy and fecal immunochemical testing (FIT). The registry describes this as a randomized trial of screen-resistant patients at the Manhattan VA Medical Center. The primary outcome counted participants who underwent screening within 6 months of the initial letter.

This question concerns screening behavior after an offer, not the accuracy of the blood test, cancer detection, or the health effects of screening. The registry’s primary outcome is defined as the percentage of participants undergoing screening in the intervention group versus the control group. The posted outcome data record counts in each group, alongside a risk-difference estimate. The trial also set out to examine colonoscopy follow-up after a positive blood-based test and participants’ views about screening choices. The registry record does not report every planned measure in detail.

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. It lists an enrollment of 359 and a completed status. The start date is 2018-10-11, and the primary completion date is 2020-12-31. The condition listed is colorectal cancer. The phase is recorded as NA, which is consistent with the trial being about a screening strategy rather than a drug phase.

Participants were randomized 1:1 to the Septin9 group or control group, according to the trial summary. The control group received a letter stating that screening was not up to date and encouraging the patient to contact the study number to choose colonoscopy or FIT. The Septin9 group received the same encouragement and was additionally offered a blood test. The description says the letter included instructions to call the study number to schedule; further operational details are not reported in the registry record. The control-arm description says callers could speak with a research assistant trained in patient navigation, who could facilitate referrals.

The primary outcome was screening within 6 months of the initial letter. A secondary screening-strategy outcome was recorded at 12 months. Other listed secondary outcomes concern colonoscopy follow-up in the intervention group, self-reported willingness to take the blood test, and reported advantages or reasons for refusing it. The registry record posts selected secondary outcome data but does not report analyses for all listed outcomes.

Because masking was absent, participants and study personnel were not masked to group assignment according to the registry entry. Random allocation can help balance groups at assignment, but it does not itself prevent differences in later behavior or outcome ascertainment. Details of sequence generation, concealment, participant flow, and 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: The target enrollment specified in the protocol is 360 participants. Actual enrollment was 359 participants.

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.

Population: Individuals who are eligible for colorectal cancer screening and have previously declined colonoscopy and FIT.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Who Undergo Screening Within 6 Months of Outreach, measured over 6 months.

The primary endpoint counts participants who underwent screening within 6 months after the initial outreach letter. The registry describes the comparison as the percentage completing screening in the Septin9 group versus the control group, and the posted results give the number of participants with the outcome and the number in each group.

This endpoint addresses the trial’s central behavioral question: whether offering another screening option was followed by a different level of screening uptake among people who had declined colonoscopy and FIT. It is a process outcome. It does not measure whether colorectal cancer was present, whether the screening tests detected disease, or whether screening changed later health outcomes. Those questions require different outcomes and follow-up.

The registry reports 17 participants with screening in the control group, out of 178, and 31 in the Septin9 group, out of 181. The corresponding posted outcome proportions are 0.096 and 0.171. The estimated risk difference is 0.076, with a confidence interval from 0.006 to 0.146. The unadjusted p-value is 0.035. These figures describe the observed group contrast for the defined follow-up period; interpretation also depends on the trial’s methods, outcome ascertainment, and the limits of the registry record.

“Screening” is the broad outcome named in the registry. The exact operational rules for determining which completed actions counted toward this endpoint are not reported in the registry record. That distinction matters when interpreting an outcome that can include more than one screening strategy.

7. Results Posted in the Registry

• Septin9: 17.1% (31/181) versus 9.6% (17/178) on control; risk difference 7.6 percentage points (95% CI 0.6 to 14.6), risk ratio 1.79 (1.03–3.12); unadjusted two-proportion z-test p = 0.035.

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.

Percentage of Participants Completing Screening Strategy

• 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:
  • Septin9: 14.9% (27/181) versus 9.0% (16/178) on control; risk difference 5.9 percentage points (95% CI -0.7 to 12.6), risk ratio 1.66 (0.93–2.97); unadjusted two-proportion z-test p = 0.084.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Septin9 and the control. The interval gives the range of effects that remain compatible with the data.

Self-reported Most Common Advantages of Blood Test on Questionnaire

• 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:
  • No Special Preperation: 40.8% (31/76) versus 60.5% (46/76) on control; risk difference -19.7 percentage points (95% CI -35.3 to -4.2), risk ratio 0.67 (0.49–0.93); unadjusted two-proportion z-test p = 0.015.
  • Accustomed to Blood Tests: 39.3% (24/61) versus 60.5% (46/76) on control; risk difference -21.2 percentage points (95% CI -37.6 to -4.7), risk ratio 0.65 (0.45–0.93); unadjusted two-proportion z-test p = 0.014.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for No Special Preperation than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Accustomed to Blood Tests than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary screening-uptake question in two directions. The later screening-strategy measure asks whether the pattern persists over a longer follow-up window. Questionnaire outcomes address attitudes toward the blood test, including stated advantages and willingness, while the colonoscopy follow-up outcome concerns the next step after a positive blood-based test. These measures provide context, but they do not all represent the same kind of evidence: completed screening is a behavior, whereas questionnaire responses are self-reported views.

The later screening-strategy estimate points in the same direction as the primary estimate, but its confidence interval includes zero. That makes the secondary result less conclusive about whether a difference exists at that time point. Questionnaire responses describe what respondents reported, not whether they subsequently completed screening. The posted results do not provide analyses for every secondary outcome listed in the registry, including several outcomes named in the study description. Details of the number of respondents for all such measures, and of any missing responses, are not reported in the registry record.

Unadjusted secondary findings carry less weight because testing multiple outcomes increases the chance that at least one result will appear unusual by chance. General statistical explanation: multiplicity can be handled in several ways, but the appropriate approach depends on a prespecified analysis plan. The registry record does not report a multiplicity strategy or identify which secondary outcomes, if any, were designated confirmatory. As a result, secondary p-values should be viewed as exploratory rather than as independent confirmation of the primary finding.

The overall pattern is therefore best read as a primary comparative result accompanied by secondary context of varying completeness and certainty. The secondary material does not establish the mechanism behind screening uptake, nor does it determine whether a stated preference translates into later behavior. Interpretation should give priority to the prespecified primary outcome if such status was established in the protocol; the protocol’s analysis hierarchy is not reported in the registry record.

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

• Percentage of Participants Completing Screening Strategy
• Percentage of Participants With Colonoscopy Follow-up in Intervention Group
• Self-reported Willingness to Take Blood Test for Colorectal Cancer Screening on Questionnaire
• Self-reported Most Common Advantages of Blood Test on Questionnaire
• Self-reported Most Common Reasons for Refusing Blood Test on Questionnaire in Intervention Group

9. Statistical Interpretation

10. Statistical Methods Explained

The principal comparison is between the proportion of participants with the screening outcome in each randomized group. For a binary outcome, each participant is classified as having or not having the event during the specified follow-up. The registry posts event counts and group sizes, then reports a risk difference comparing the observed proportions. A risk difference is an absolute contrast on the proportion scale: it describes how far apart the group proportions are, rather than how many times as large one is relative to the other.

What does randomization contribute?

Random assignment is intended to make the groups comparable, on average, at the point of allocation. It supports a causal interpretation more than a nonrandom comparison would, but it does not guarantee that the realized groups are identical in every characteristic. Nor does randomization resolve issues such as incomplete outcome recording, departures from assigned outreach, or differences in how outcomes are assessed. The registry identifies the allocation as randomized and states that allocation was 1:1. Details of sequence generation and allocation concealment are not reported in the registry record.

The trial is described as open-label, meaning masking was not used. General statistical consideration: when people know the group assignment, that knowledge can influence behavior or reporting, especially for outcomes involving choices and self-report. The primary outcome is a screening action, but the registry record does not explain how completion was verified or whether ascertainment differed between groups. Those details are not reported in the registry record.

How should the risk difference be read?

The observed control proportion is 0.096 and the Septin9 proportion is 0.171. The posted risk difference is 0.076, and the confidence interval ranges from 0.006 to 0.146. The direction of the estimate indicates a higher observed proportion in the Septin9 group. This is an absolute comparison of the recorded outcome, not a measure of test sensitivity or of the probability that a participant had cancer.

The registry also posts relative measures: the risk ratio is 1.793, with a confidence interval from 1.03 to 3.121, and the odds ratio is 1.957, with a confidence interval from 1.04 to 3.682. These quantities express group contrasts on different scales. Risk ratios compare proportions directly; odds ratios compare odds, which are formed from the event and non-event proportions. The scales answer related but distinct questions, and the risk difference remains a direct description of the absolute separation in the observed proportions. The registry does not identify a preferred measure beyond posting the risk-difference comparison.

What does the p-value describe?

The primary unadjusted p-value is 0.035. In general, a p-value describes how compatible the observed data are with a specified null model, under the assumptions of the test used. Smaller p-values indicate less compatibility with that null model, but the value does not measure the size or practical importance of an effect and is not the probability that the null hypothesis is true. The specific test, its assumptions, and any prespecified analysis procedures are not reported in the registry record. The reported p-value is labelled unadjusted, so it should not be mistaken for a result adjusted for multiple outcomes or comparisons.

A confidence interval gives a range of estimates compatible with the data under the interval procedure’s assumptions. General statistical explanation: repeated use of a specified interval method would capture the underlying parameter at its stated confidence level in the long run, if the model assumptions held. The confidence interval does not account automatically for every source of uncertainty, such as an outcome definition that is unclear or selective reporting. The method used to construct the posted intervals is not reported in the registry record.

Why do follow-up time and outcome definitions matter?

The primary outcome concerns screening within 6 months. A secondary screening-strategy outcome is recorded at 12 months. These time frames answer different questions: the earlier measure reflects completion in the initial follow-up window, while the later measure concerns a longer period. The record does not explain whether the 12-month measure includes, excludes, or otherwise relates to participants counted at the earlier time point. The outcomes should not be treated as interchangeable.

General statistical consideration: binary outcomes discard timing and detail by reducing each participant’s experience to whether the event was recorded within the defined period. That can be appropriate for an uptake question, but it does not show when screening occurred or which specific screening strategy was used. The registry title and outcome descriptions refer to screening, while the exact endpoint rules are not reported in the registry record.

What is known about the analysis plan?

The registry lists no reported analyses for the posted secondary outcomes. It does not report the primary statistical model, covariate adjustment, handling of missing outcomes, analysis population, interim analyses, or the trial’s original sample-size justification. These are distinct from the planning illustrations based on the observed effect. Without the prespecified analysis details, the registry results can be described, but the analysis cannot be fully audited against an original protocol from this record alone.

General statistical consideration: estimates and tests depend on assumptions about sampling, outcome measurement, and analysis. For binary outcomes, the count of participants with an event is central, while the group size determines how much information the observed proportion contains. A confidence interval indicates sampling uncertainty under its method; it does not correct for unreported missingness, bias in ascertainment, or limitations in generalizability. The numerical results should therefore be interpreted together with the trial setting, the open-label design, and the incomplete analytic detail in the registry record.

11. Confidence Intervals and Precision

The primary risk-difference estimate is 0.076, with a confidence interval from 0.006 to 0.146. The interval indicates that the data are compatible with a range of possible absolute differences, from a comparatively small positive contrast to a larger one. Its width reflects uncertainty in the estimate; it does not pinpoint a single underlying value.

The confidence interval does not include zero, the value corresponding to no difference on the risk-difference scale. The primary unadjusted p-value is 0.035. These results are consistent with a higher observed screening proportion in the Septin9 group for the primary follow-up period, but precision remains limited: the interval spans a meaningful range of possible effects. No confidence-interval construction method is reported in the registry record, so the interval’s assumptions cannot be checked from the posted entry.

The posted relative measures give additional perspectives. The risk ratio is 1.793, with a confidence interval from 1.03 to 3.121; the odds ratio is 1.957, with a confidence interval from 1.04 to 3.682. Their intervals also span a range of values, and they should not be interpreted as interchangeable with the absolute risk difference.

For the 12-month screening-strategy outcome, the risk-difference estimate is 0.059, with a confidence interval from -0.007 to 0.126. This interval includes zero and allows for a range that includes no difference. General statistical explanation: an interval is not a guarantee that the true effect lies within its endpoints, nor does it incorporate every possible source of uncertainty. It summarizes uncertainty under the interval method, whose details are not reported in the registry record.

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 the observed effect, not the trial’s original design assumptions. For these binary outcomes, the figures are participants per arm, not a total number of events. The listed 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 trial’s original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column describes the planned number of participants per arm for a design that would have an 80% chance of detecting the selected effect under the stated assumptions, if that effect and the assumptions were correct. The 90% power column describes the corresponding planning target for a higher chance of detecting that effect. These are design calculations, not results about the probability that the trial’s conclusion is correct.

The rows for 100%, 75%, and 50% of the observed effect ask how the required sample size would change if the target effect were the full observed estimate or a smaller fraction of it. Smaller effects require more participants per arm to detect, all else equal. The posted figures illustrate that relationship for the primary outcome and selected secondary comparisons. They do not describe the number actually enrolled for every comparison, and they should not be used to infer that the completed trial had a particular probability of finding an effect. This is not observed power.

General statistical explanation: sample-size planning depends on the outcome frequency, target effect, significance level, allocation, and calculation method. If any of these differ from the planning assumptions, the resulting figures may not apply. Because the calculations use the observed effect as their starting point, they are best read as hypothetical planning scenarios rather than evidence that the original trial was adequately or inadequately sized.

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 = 0.096; treatment proportion p₁ = 0.171; average p̄ = 0.133.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4808 = 0.9424.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4778 = 0.4022.
4. n = (0.9424 + 0.4022)² / (0.0758)² = 314.9, rounded up to 315 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 <- 0.0955056179775281                          # control proportion
p1 <- 0.171270718232044                          # 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(3598166)
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 = 315 (80% power), 422 (90% power)
 75% of observed effect: n per arm = 527 (80% power), 705 (90% power)
 50% of observed effect: n per arm = 1,108 (80% power), 1,483 (90% power)
power.prop.test: 314.9 
Simulated power at n = 315 per arm: 0.804 (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 identifies a primary outcome and several secondary outcomes, but it does not report a complete statistical analysis plan. In particular, a strategy for handling multiple comparisons is not reported in the registry record. The primary p-value is labelled unadjusted. The posted secondary analyses are also not accompanied by reported multiplicity adjustments, and the registry lists no reported analyses for the secondary outcomes. These gaps limit how confidently secondary findings can be treated as confirmatory.

General statistical explanation: when investigators examine multiple outcomes, each test creates an opportunity for a chance finding. If many results are considered together, interpreting a single unadjusted p-value as though it came from the only planned test can overstate the strength of evidence. Prespecifying a hierarchy or an adjustment method can help clarify how results should be interpreted. Whether such procedures were used in this trial is not reported in the registry record.

The record also does not report how missing outcome data were handled, whether any participants were excluded from analyses, or which analysis population was used. It is therefore not possible from the registry entry to determine whether the primary analysis followed intention-to-treat principles, whether it included only participants with observed outcomes, or whether another population was analyzed. Participant flow and reasons for missing outcome information are not reported in the registry record.

For a behavioral outcome, missingness can matter if outcome status is unavailable more often in one group or is related to whether screening occurred. General statistical consideration: analyses of only observed outcomes can be biased when the availability of outcome data is associated with the outcome itself or with group assignment. The registry record does not provide the information needed to evaluate that possibility.

Interim analyses, stopping rules, covariate adjustment, and the original sample-size justification are also not reported in the registry record. The stated planning illustrations based on the observed effect do not substitute for the trial’s original design documentation. These absences do not change the posted counts, but they constrain assessment of how the results were selected, analyzed, and related to the initial study plan.

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 reports serious adverse events among 0 of 178 participants at risk in the control group and 0 of 181 participants at risk in the Septin9 group. Other adverse events are likewise listed as 0 in each group, with 178 and 181 participants at risk, respectively. These are counts in the registry record; the record does not provide event descriptions because no serious adverse-event terms are listed.

Deaths are reported separately: 3 in the control group and 2 in the Septin9 group. The registry entry does not attribute these deaths to the intervention, the blood test, or any other cause. These counts alone cannot establish a safety difference, particularly without causes, timing, individual-level details, or a reported comparative analysis.

General statistical explanation: zero recorded events does not prove that an event is impossible or that risk is absent. It means that no events of that category were recorded among the listed participants at risk in this registry report. The entry does not give detailed safety-monitoring methods, definitions beyond the serious and other event categories, or a statistical analysis of safety outcomes. Safety conclusions should therefore remain limited to the reported counts.

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

The primary result describes screening completion after a specific outreach approach among patients who had declined colonoscopy and FIT at the Manhattan VA Medical Center. The observed screening proportion was higher in the Septin9 group than in the control group during the 6-month primary follow-up. The estimated risk difference was 0.076, with a confidence interval from 0.006 to 0.146. This is a comparison of the groups’ observed screening outcomes in this trial, not proof of a general effect in every population or care setting.

The intervention was an offer embedded in outreach that also encouraged colonoscopy or FIT. The result cannot isolate the effect of the blood test from the effects of the letter, additional choice, scheduling instructions, or other aspects of study contact. The registry record does not report a component comparison that would distinguish these possibilities.

The outcome is screening completion, not cancer detection, diagnostic accuracy, cancer incidence, mortality, or long-term health. The trial’s stated aims included evaluating colonoscopy after a positive blood-based test and describing endoscopic findings, but the registry record does not post results for all of those aims. The primary result therefore cannot establish the clinical consequences of screening or of follow-up after a positive test.

The posted data also do not show what would happen among people who had not refused both colonoscopy and FIT, or among patients in other settings. The study was conducted at the Manhattan VA Medical Center, and detailed participant characteristics are not reported in the registry record. The findings should not be generalized beyond the population and context represented by the trial without additional evidence.

Finally, a p-value is not a measure of clinical importance, and a confidence interval does not remove uncertainty about outcome ascertainment, missing data, or analysis choices. The registry record provides useful counts and estimates but does not report several details needed for a full appraisal of the protocol and analysis. The result is best understood as a context-specific estimate of screening behavior with finite precision.

17. Why This Trial Matters Statistically

This trial is statistically notable because it evaluates a screening behavior among people described as having refused two established screening options. For that population, the question is not only whether a test can be performed, but whether offering another option is associated with subsequent screening. The randomized comparison makes the outcome relevant to an intervention strategy rather than simply describing preferences in a group offered the blood test.

The endpoint also illustrates the importance of matching a statistical question to a meaningful process outcome. Screening completion within 6 months captures an action after outreach. It does not answer whether the test detects disease accurately or whether screening changes later health. Keeping those outcomes distinct prevents a behavioral result from being interpreted as evidence about clinical effectiveness.

The posted risk difference and its confidence interval show why both effect size and precision matter. The point estimate gives the observed absolute contrast, while the interval communicates that a range of magnitudes remains compatible with the data. Reporting the group counts, the estimate, and its uncertainty gives a fuller account than a p-value alone.

The trial also illustrates limits of registry reporting. Randomization and the primary outcome are described, but details of the statistical plan, missing-data handling, analysis population, and multiplicity approach are not reported in the registry record. Those details affect how results can be evaluated and how much weight to assign secondary findings. A complete interpretation depends not only on numerical results but also on transparent methods and clearly defined outcomes.

Finally, the setting and eligibility focus are central to statistical generalization. Results among patients who had declined colonoscopy and FIT may not represent screening behavior in other patient groups. Statistical evidence is most useful when its target population, outcome definition, time frame, and uncertainty are kept explicit.

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 trial addresses a specific group: patients who had refused both colonoscopy and FIT within the past 6 months. That focus is relevant to the stated screening question but limits how directly the results apply to people who have not declined those options. The study was conducted at the Manhattan VA Medical Center; the registry record does not describe other sites or provide detailed participant characteristics that would help assess how well the results transfer to other settings.

The design was open-label. Participants and study personnel knew the assigned outreach approach, and the primary outcome involves participant behavior. The registry does not explain how screening completion was verified or whether the same ascertainment procedures were applied across groups. Outcome definitions beyond the brief description are not reported in the registry record.

The intervention combined an offer of the blood test with encouragement to consider colonoscopy or FIT. Because the record does not describe a comparison that separates these components, the observed contrast cannot be assigned specifically to the test offer, the additional choice, or another aspect of outreach. Further details of scheduling, uptake, and follow-up procedures are not reported in the registry record.

The posted primary result has a confidence interval from 0.006 to 0.146, indicating uncertainty about the size of the group difference. The later screening-strategy outcome has an interval from -0.007 to 0.126. The registry does not report missing-data handling, participant flow by outcome, the analysis population, or the original statistical analysis plan. Results for some listed secondary aims are not posted as analyses, and a multiplicity approach is not reported.

Finally, the primary endpoint is a screening-process outcome. The posted result does not establish test accuracy, cancer detection, or downstream clinical outcomes. The registry record also does not provide detailed results on diagnostic colonoscopy findings after a positive blood test. These limits define what can be concluded from the posted evidence.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Assessing the Effect of a Blood-based Colorectal Cancer Screening Test on Screening Adherence and Colonoscopy Completion — NCT03598166.
• Registry record last updated 2023-01-05; status last verified 2022-12.
• Results first posted 2023-01-05.
• 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

NCT03598166 is a completed, randomized, open-label, parallel-group trial titled “Assessing the Effect of a Blood-based Colorectal Cancer Screening Test on Screening Adherence and Colonoscopy Completion.” Enrollment was 359. The study compared outreach offering Septin9 with control outreach encouraging colonoscopy or FIT among patients who had refused both options. The primary outcome was screening within 6 months of the initial letter.

The primary risk-difference estimate was 0.076, with a confidence interval from 0.006 to 0.146 and an unadjusted p-value of 0.035. The registry also posts a 12-month screening-strategy outcome and selected questionnaire results. Serious and other adverse-event counts were zero in both groups; deaths were recorded as 3 in control and 2 in Septin9, without causal attribution.

The registry record does not report the full analysis plan, handling of missing data, analysis populations, multiplicity strategy, or original sample-size justification. Conclusions are therefore limited to the posted screening-behavior results in this trial setting.