Health Education Materials With/Out a Physical Activity Program for Patients Who Have Undergone Treatment for High-Risk Stage II or Stage III Colon Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Health Education Materials With/Out a Physical Activity Program for Patients Who Have Undergone Treatment for High-Risk Stage II or Stage III Colon Cancer (NCT00819208), a randomized na study. The primary outcome is Disease-free Survival.

2. Clinical Question

The study rationale was that a physical activity program might affect recurrence as well as fitness, psychological well-being, and quality of life after colon cancer treatment. The central comparison isolates the addition of the program to the shared health education materials, rather than comparing education with no education. The registry also lists overall survival as a secondary outcome, assessed at eight years after randomization. The posted outcomes therefore cover both a composite measure of disease-free survival and survival from any cause. They address differences between the randomized groups; they do not, by themselves, establish which aspects of a program or its components account for any observed group contrast.

3. Trial Design

The registry describes a randomized, parallel-group trial with no masking. It is marked completed and records enrollment of 889 participants. The official title and brief summary describe the study as Phase III, while the phase classification is recorded as NA. The sponsor is the Canadian Cancer Trials Group. The recorded start date is 2009-06-02, and the primary completion date is 2025-02-07.

Participants were assigned to a physical activity program plus general health education materials or to general health education materials alone. The arm descriptions identify those as the intervention and control groups, respectively. The primary outcome population is all patients randomized, and the arm sizes listed for the primary outcome are 445 and 444. Because the trial was unmasked, participants and study personnel were not masked to assignment according to the registry. The registry does not report further details about allocation procedures or whether outcome assessors were masked.

The intervention inventory includes exercise, counseling, educational materials, laboratory biomarker analysis, questionnaire administration, and study of socioeconomic and demographic variables. It also lists fatigue assessment and management and quality-of-life assessment. These entries describe the range of listed study activities, but do not establish the exact schedule, intensity, or uptake of the physical activity program. Those intervention-delivery details are not reported in the registry record.

The primary endpoint is disease-free survival at five years after randomization. Overall survival at eight years after randomization is the posted secondary outcome. A log-rank analysis is reported for each outcome. Details of additional design features, including the original sample-size justification, allocation concealment, and any planned interim analyses, 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

Analysis population for the primary outcome, as defined in the registry: All patients randomized.

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: All patients who were randomized to the study.

6. Primary Endpoint

The registry lists the primary outcome as Disease-free Survival, measured over 5 Years after randomization.

Disease-free survival is defined as the time from randomization to the first of the following events: recurrent local or distant colon cancer, a new primary colorectal cancer, a second primary cancer, or death from any cause. The registry presents the primary outcome as the five-year disease-free survival rate, expressed as a percentage of participants, with a 95% confidence interval. The stated population is all patients randomized.

This composite endpoint brings recurrence, additional primary cancers, and death into a single outcome. In general, a disease-free survival measure can capture several important events within a follow-up period and can use information about when an event occurred, rather than only whether an event was ever recorded. That is a general statistical rationale for time-to-event endpoints, not a claim about the trial’s design rationale beyond the registry description. The registry definition also makes clear that death from any cause counts as an event, not only death attributed to colon cancer.

The five-year rate and the reported log-rank analysis are related summaries, but they are not identical statistical quantities. A rate describes the estimated proportion disease-free at the specified time; the log-rank analysis compares event-time patterns across groups. Details of censoring, handling of participants lost to follow-up, and the estimation method used for the five-year rates are not reported in the registry record.

7. Results Posted in the Registry

• General Health Education Materials: 73.9% (328/444) versus 80.2% (357/445) on control; risk difference -6.4 percentage points (95% CI -11.9 to -0.8), risk ratio 0.92 (0.86–0.99); unadjusted two-proportion z-test p = 0.024.

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.

Overall Survival

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • General Health Education Materials: 83.1% (369/444) versus 90.3% (402/445) on control; risk difference -7.2 percentage points (95% CI -11.7 to -2.8), risk ratio 0.92 (0.87–0.97); unadjusted two-proportion z-test p = 0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for General Health Education Materials than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Overall survival is the posted secondary outcome, assessed at eight years after randomization. The broad direction of its comparison aligns with the primary disease-free survival result: the arm receiving the physical activity program plus education has the higher posted survival estimate, and the sponsor-reported hazard ratio is below 1 with that arm listed first. This directional consistency offers context across outcomes, but does not turn the secondary result into a second primary endpoint.

The outcomes are related but not identical. Disease-free survival includes recurrence and new primary cancers as well as death from any cause, whereas overall survival concerns death from any cause. Agreement in direction across these measures may be informative, but each estimate has its own endpoint definition, follow-up period, and uncertainty. The secondary result should not be treated as an independent replication of the primary finding, since both arise from the same randomized trial and participant groups.

Unadjusted secondary results carry less weight when multiple outcomes or comparisons are examined. In general, testing multiple hypotheses increases the chance that at least one result appears statistically notable even when there is no corresponding effect. Methods such as prespecifying a hierarchy or adjusting for multiplicity can address that issue, but the registry does not report whether such procedures were planned or applied. The posted secondary result is therefore best considered supportive and descriptive rather than definitive confirmation.

The registry does not report further secondary outcomes beyond overall survival in the posted results, nor does it document a multiplicity strategy. It is not possible to infer from the record how the sponsor intended to interpret secondary testing within the complete trial analysis plan. The pattern is consistent across the posted primary and secondary outcomes, while the evidential status of the secondary comparison remains more limited.

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

• Overall Survival

9. Statistical Interpretation

10. Statistical Methods Explained

The posted results combine a time-to-event comparison with estimates of the proportion of participants disease-free at a specified follow-up time. Understanding the distinction helps explain why both a five-year rate and a hazard ratio can be reported for the same endpoint. The registry identifies the sponsor analysis as a log-rank test with a hazard ratio, while the unadjusted re-calculation uses the posted summary rates.

What does the log-rank analysis compare?

In general, a log-rank test compares the pattern of event times between groups over follow-up. It is designed for time-to-event data, in which the event and its timing matter, and where some participants may have incomplete follow-up without an observed event. The test uses information across the follow-up period rather than reducing the outcome to a yes-or-no status at a single time point. The registry does not give details of how censoring was handled, so those implementation choices are not reported in the registry record.

The reported hazard ratio summarizes a relative event hazard between the randomized groups under a time-to-event model. A value below 1, with the physical activity program group first, corresponds to a lower estimated event hazard in that group. A hazard ratio is not a ratio of the five-year percentages, and it is not a direct estimate of the difference in the probability of an event at five years. Its interpretation also depends on the model and assumptions; the registry does not report a proportional-hazards assessment or related diagnostics.

How does a confidence interval help?

In general, a confidence interval describes the range of estimates compatible with the data under the method used, at the stated confidence level. It conveys uncertainty around an estimate and should be read alongside the point estimate. A wider interval indicates less precision than a narrower interval on the same scale. A 95% confidence interval does not mean there is a 95% probability that the particular interval contains the true value; that is not the usual frequentist interpretation.

For the sponsor’s hazard ratio, the 95% confidence interval is 0.55 to 0.94. It is below 1 throughout, matching the direction of the point estimate. The five-year rates also have 95% confidence intervals, reflecting uncertainty in each group’s rate. Comparing two separate rate intervals by eye is not the same as examining a confidence interval for the between-group contrast.

What does the binary re-calculation add?

The unadjusted re-calculation treats the posted five-year outcomes as a binary contrast and expresses the comparison as a risk difference. It is a simple comparison based on the summary rates rather than a re-analysis of participant-level event times. The associated p-value is unadjusted, meaning it is not modified for other outcome tests or comparisons. Such a calculation can help readers understand the absolute contrast represented by the rates, but it does not supersede the sponsor’s time-to-event analysis.

The fact that the binary and time-to-event analyses are related does not require their p-values or estimates to be identical. They use different summaries and methods. The time-to-event test incorporates timing over follow-up, while the binary calculation focuses on status at the stated time point. The registry does not report adjusted binary analyses, covariate adjustment, or participant-level data that would allow those approaches to be compared in greater detail.

What does a p-value mean?

In general, a p-value measures how incompatible the observed data are with a specified null hypothesis, assuming the analysis model and its assumptions. It is not the probability that the null hypothesis is true, nor does it measure the probability that the findings arose “by chance.” A small p-value does not reveal whether an effect is large, clinically important, unbiased, or reproducible. The estimate and its confidence interval are needed to assess magnitude and precision.

The sponsor-reported log-rank p-value is 0.02, and the unadjusted binary re-calculation has p = 0.024. These values arise from different analyses and should be attributed to their respective methods. The registry does not report a prespecified threshold, a multiplicity adjustment, or the complete analysis plan, so claims about how the sponsor classified the results under its original plan cannot be verified from the record.

Why can over-dispersion matter?

In general, over-dispersion occurs when data vary more than a statistical model expects. If a model assumes less variability than the data contain, standard errors can be too small and confidence intervals too narrow, potentially making evidence appear stronger than it is. The outcomes posted for this trial are survival rates and time-to-event comparisons, and the registry does not report a model or analysis involving a dispersion parameter. Over-dispersion is therefore a general statistical concept, not a reported feature of these analyses.

The registry’s methods description is limited. It identifies the primary outcome, its time frame, the log-rank method, hazard ratio, confidence interval, and p-value. It does not report covariate adjustment, stratification factors, missing-data procedures, sensitivity analyses, model diagnostics, or interim analyses. Those omissions constrain how fully readers can assess implementation and robustness; they do not demonstrate that a particular procedure was or was not used.

11. Confidence Intervals and Precision

Precision concerns how tightly the data estimate an outcome or comparison. The five-year disease-free survival estimate in the physical activity program plus education arm is 80.3%, with a 95% confidence interval from 76.0% to 83.9%. In the education-alone arm, the estimate is 73.9%, with a 95% confidence interval from 69.3% to 78.0%. These intervals communicate uncertainty around each arm’s rate; they do not by themselves provide the confidence interval for the between-arm difference.

The sponsor-reported hazard ratio is 0.72, with a 95% confidence interval from 0.55 to 0.94. The interval excludes 1 and spans a range of relative hazard estimates. Its width is relevant to how precisely the relative comparison is estimated. It should be interpreted on the hazard-ratio scale, not as an interval for percentage-point differences in the five-year rates.

In general, a confidence interval is affected by the amount of information available and the variability of the observations, as well as the statistical method. A larger sample does not guarantee a narrow interval if events are uncommon, follow-up is incomplete, or observations are variable. The registry lists 445 and 444 participants in the primary outcome arms, but does not report the number of participants with complete five-year follow-up or the detailed event and censoring data underlying the estimates.

Confidence intervals are not guarantees that the true value lies within the displayed limits, nor do they show the range of individual participant outcomes. They describe uncertainty about a group-level parameter under the analysis method. The limits should be read with the point estimate and with the endpoint definition in mind. Because the registry does not provide further estimation details, readers cannot assess all sources of uncertainty or reproduce the intervals from participant-level data.

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 sample-size display is a planning illustration based on the observed effect, not a report of the trial’s original design calculation. For the binary outcomes, the figures are participants per arm, not total participants and not total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers detecting the stated fraction of the observed effect. Smaller effects require more participants per arm to reach the same target power.

The 80% power column gives the number of participants per arm in the planning calculation for a design with an 80% chance of rejecting the null hypothesis if the assumed effect is real, under the stated assumptions. The 90% power column gives the corresponding per-arm number for a 90% chance. These are design-planning quantities, not guarantees about results in a future study; actual power depends on the true effect, outcome variability, follow-up, and analysis conditions.

The rows for 100%, 75%, and 50% of the observed effect illustrate how the required participant count changes as the assumed effect becomes smaller. The observed effect is used only as the starting point for this illustration; assuming a fraction of it is a planning choice, not evidence that the effect will recur at that size. The sample-size assumptions explicitly distinguish time-to-event planning, for which the display gives total events using the Schoenfeld method, from other outcomes, for which it gives participants per arm. The posted outcomes use binary rate calculations for the sample-size illustration, so their entries are per-arm participant counts.

These figures are not observed power. Observed power calculated from the estimated effect after a trial is complete does not add useful information beyond the estimate, confidence interval, and test result. The original trial’s sample-size justification and design assumptions are not reported in the registry record; the illustration should not be mistaken for that original plan.

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 = 0.802; treatment proportion p₁ = 0.739; average p̄ = 0.770.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5947 = 1.1656.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5930 = 0.4991.
4. n = (1.1656 + 0.4991)² / (-0.0635)² = 687.1, rounded up to 688 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 <- 0.802247191011236                          # control proportion
p1 <- 0.738738738738739                          # 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(819208)
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 = 688 (80% power), 920 (90% power)
 75% of observed effect: n per arm = 1,193 (80% power), 1,596 (90% power)
 50% of observed effect: n per arm = 2,615 (80% power), 3,500 (90% power)
power.prop.test: 687.1 
Simulated power at n = 688 per arm: 0.799 (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-reported primary analysis is a log-rank comparison, with a hazard ratio of 0.72, a 95% confidence interval from 0.55 to 0.94, and p = 0.02. This is the registry’s stated time-to-event result and uses the event-time information for disease-free survival. The physical activity program plus education arm is listed first in the reported group comparison.

The simple unadjusted re-calculation instead uses the posted five-year summary rates to compare the arms as a binary outcome. Its direction is consistent with the sponsor-reported result, and its unadjusted p-value is 0.024. The two analyses are not interchangeable: one summarizes the relative event hazard over follow-up, while the other compares outcome rates at the stated time point. Their estimates and p-values need not match exactly.

The registry record does not flag a discrepancy between the sponsor analysis and the re-calculation. The sponsor result remains the reported analysis, while the re-calculation offers a transparent, unadjusted comparison based on the summary statistics. The record does not provide the participant-level data, full analysis plan, or additional methodological detail needed to reproduce the sponsor analysis independently or determine whether further adjustments were used.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when an analysis tests more than one outcome, time point, subgroup, or comparison. In general, as the number of statistical tests increases, so does the opportunity for a result to cross a conventional significance threshold by chance, even if no effect exists. Prespecified outcome hierarchies, adjusted significance thresholds, or other multiplicity procedures can help control that risk. The registry does not report a multiplicity adjustment or a plan for interpreting the primary and secondary tests together.

The primary disease-free survival outcome and secondary overall survival outcome are both posted with analyses. The record does not establish whether these were the only analyses planned, whether additional subgroup or sensitivity analyses were prespecified, or whether a testing hierarchy was used. The unadjusted p-values should therefore be read as results of their individual analyses, not as multiplicity-controlled evidence across all outcomes that may have been considered.

The primary population is described as all patients randomized, which is consistent with an intention-to-treat population in broad terms. However, the registry does not explicitly describe an intention-to-treat analysis rule or explain how participants with missing outcome information were handled. It also does not report the number of participants contributing information at each follow-up time, reasons for missing data, censoring rules, or sensitivity analyses for incomplete follow-up. The randomized arm sizes alone do not establish that every participant contributed complete five-year outcome data.

These omissions matter because missing outcome information and censoring can affect time-to-event estimates if they are related to prognosis or differ between groups. In general, survival methods can retain partial follow-up information through censoring, but their interpretation depends on assumptions and implementation. The registry does not provide enough detail to evaluate those aspects for this trial. The missing information limits independent assessment; it is not evidence that the analysis was necessarily biased or improperly conducted.

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 5% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event counts list zero affected participants in each group among those at risk: 428 in the physical activity program plus education group and 461 in the education-alone group. No serious adverse event terms are listed. The registry also reports other adverse events affecting 351 of 428 participants in the program group and 352 of 461 in the education-alone group. Deaths are listed as 41 and 66, respectively.

These are counts, not rates adjusted for follow-up time, and the at-risk denominators differ from the randomized arm sizes of 445 and 444. The registry does not report why the denominators differ, event severity definitions beyond the serious-event category, timing, duration, or whether events were judged related to the intervention. The death counts should not be interpreted as evidence of causation or as a separate treatment effect without fuller definitions and analysis.

Zero serious adverse event reports in these summaries does not establish that no safety events occurred outside the recorded categories or reporting period. The figures should be read as the registry’s posted adverse-event summaries, with their denominators and reporting limitations kept in view.

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

The posted results describe a randomized comparison of a physical activity program added to general health education materials against the same education materials alone. At five years, the disease-free survival estimate is higher in the program arm, and the sponsor’s log-rank analysis reports a hazard ratio below 1 with a confidence interval that excludes 1. The unadjusted binary re-calculation points in the same direction. The secondary overall survival comparison has a broadly consistent direction.

These findings are estimates for groups, not predictions for individual participants. They do not show that every participant benefited, that every participant completed the program, or that the physical activity component alone produced the observed contrast. The two arms differ by the addition of a program package, and the registry does not report enough intervention-fidelity information to identify which elements were received or how participation varied.

A statistically notable result is not automatically a measure of clinical importance. The size of an effect, its uncertainty, the endpoint’s relevance, possible harms, feasibility, and the completeness of the evidence all matter to a broader interpretation. The registry provides outcome estimates and selected statistical results, but details about adherence, missing data, adjustment, and the full analysis plan are not reported. That limits what can be concluded about robustness and the pathway linking assignment to outcomes.

The results also do not establish that the findings apply to people outside the studied population or to different program formats. The trial concerned patients treated for high-risk stage II or stage III colon cancer and compared a particular program-plus-education strategy with education alone. The registry does not provide sufficient detail to characterize the intervention dose or implementation across settings. Interpretation should remain tied to the studied comparison and the outcomes as defined, rather than extending beyond the posted evidence.

18. Why This Trial Matters Statistically

This trial illustrates why the endpoint definition and analysis method matter when interpreting clinical results. Disease-free survival combines recurrence, new primary cancers, and death into a time-to-event outcome, while its five-year rate gives a time-specific summary. A hazard ratio and a difference between fixed-time rates answer related but distinct questions. Reporting both requires readers to keep the scale and interpretation of each estimate clear.

The record also illustrates the role of precision. Point estimates describe the observed group comparisons, while confidence intervals show uncertainty around those estimates. Statistical evidence should not be reduced to whether a p-value is below a threshold. The size and precision of the comparison, the endpoint, and the limitations of the available analysis details all contribute to interpretation.

Another statistical lesson is the distinction between a sponsor-reported time-to-event analysis and a simple unadjusted re-calculation from summary rates. A re-calculation can make a posted contrast easier to inspect, but it does not reproduce all features of a participant-level survival analysis. Keeping those analyses separate helps prevent a useful cross-check from being mistaken for the trial’s primary analysis.

Finally, the posted secondary outcome raises the familiar issue of multiplicity. A direction consistent across outcomes can add context, but it does not remove the need to know whether outcomes were prespecified or whether multiple testing was addressed. The registry record’s missing methodological details make these distinctions especially important: readers can interpret the reported estimates, while recognizing that several aspects of the analysis plan and follow-up are not documented.

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

Several trial-specific details needed for a fuller assessment are not reported in the registry record. These include the original sample-size justification, allocation concealment procedures, the physical activity program’s prescribed dose and delivery schedule, and participant adherence. Although the intervention inventory lists exercise and counseling, it does not establish how consistently participants received or completed those components.

The trial was unmasked. That is a relevant design feature for a behavioral intervention, where participants and personnel may know group assignment. The registry does not report whether outcome assessors were masked or whether any steps were taken to limit assessment or reporting effects. It also does not provide enough information to evaluate possible differences in co-interventions or behavior changes outside the assigned program.

The registry identifies all randomized participants as the primary population, but does not document the analysis rule in detail. It does not report how missing outcome data, withdrawals, censoring, or incomplete follow-up were addressed, nor does it give sensitivity analyses or model diagnostics. The absence of these details prevents a reader from assessing the robustness of the estimates to those issues.

The statistical plan is also incompletely documented. The log-rank method and hazard ratio are named, but covariate adjustment, stratification, proportional-hazards assessment, interim analyses, and multiplicity procedures are not reported. The registry’s posted adverse-event summaries do not provide event timing, attribution, or explanations for the at-risk denominators. These limitations identify unanswered questions in the record; they do not establish that the study analyses or conduct were flawed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Health Education Materials With/Out a Physical Activity Program for Patients Who Have Undergone Treatment for High-Risk Stage II or Stage III Colon Cancer — NCT00819208.
• Registry record last updated 2026-04-24; status last verified 2026-04.
• Results first posted 2026-04-24.
• 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

NCT00819208 is a completed randomized, unmasked, parallel-group trial sponsored by the Canadian Cancer Trials Group, with enrollment of 889. It compared a physical activity program plus general health education materials with education materials alone among patients treated for high-risk stage II or stage III colon cancer.

The primary outcome was five-year disease-free survival, defined by recurrence, a new primary colorectal cancer, a second primary cancer, or death from any cause. The sponsor-reported log-rank analysis gives a hazard ratio of 0.72, with a 95% confidence interval from 0.55 to 0.94 and p = 0.02. Overall survival at eight years was the posted secondary outcome. The registry does not report several details needed for a complete assessment of the original design assumptions, missing-data handling, multiplicity, or intervention adherence.