Pre-op Rectal ChemoRad +/- Cetuximab: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pre-op Rectal ChemoRad +/- Cetuximab (NCT00527111), a randomized phase 2 study. The primary outcome is Percentage of Pathologic Response Rate (pCR) With 95% Confidence Interval..

2. Clinical Question

This is a question about a pathologic finding after surgery, not a direct measure of symptoms or survival. The comparison focuses on whether adding cetuximab to the stated chemoradiotherapy regimen is associated with a different observed pCR rate. The available result is descriptive as well as comparative: each group has a percentage and a 95% confidence interval, while a risk-difference estimate and its interval summarize the between-group contrast. Those quantities should be considered together. The registry does not report the trial’s own original sample-size assumptions or a detailed statistical analysis plan, so the result should be interpreted using the posted endpoint definitions and uncertainty rather than an assumed design target.

3. Trial Design

This was a randomized Phase II trial with a parallel-group design. The registry reports enrollment of 139 participants and identifies US Oncology Research as the sponsor. The two treatment groups differed by whether cetuximab was added to pelvic irradiation and 5-fluorouracil. Random allocation creates a basis for comparing outcomes between groups, although it does not guarantee that every characteristic is balanced in a trial of this size.

The trial was unmasked: the registry lists masking as none. Participants and investigators therefore were not described as blinded to the assigned regimen. Lack of masking can matter particularly for outcomes that involve judgment or reporting; the primary outcome is based on pathologic assessment, but the registry does not describe the assessment procedures or whether pathologists were masked. Those details are not reported in the registry record.

The primary outcome is reported for the post-surgery population, with 64 participants in the chemoradiotherapy-plus-cetuximab group and 60 in the chemoradiotherapy-alone group. The registry gives enrollment as 139, but does not explain the relationship between enrollment and the primary endpoint denominators. It also does not report how participants without an evaluable surgical pathology result were handled. The denominators differ for some secondary outcomes, and reasons for those differences are not reported in the registry record.

The study is marked completed, with a start date of 2007-02 and primary completion in 2015-01. These dates describe the record; they do not supply details about recruitment pace, follow-up completeness, or protocol changes. The trial’s planned sample-size rationale, original assumptions for statistical power, interim analyses, and detailed methods for handling missing data are not reported in the registry record. The planning illustrations associated with the posted results are separate from those original design decisions.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Post surgery population

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: ITT population

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Pathologic Response Rate (pCR) With 95% Confidence Interval., measured over 5 years.

The primary endpoint is the percentage of participants with a pathologic complete response, or pCR, in the post-surgery population. The registry defines pCR as no pathologic evidence of invasive disease at the primary site in the bowel wall or in examined mesorectal tissue and/or lymph nodes. A percentage expresses how frequently this specified finding occurred among the participants included in each group’s endpoint denominator.

Pathologic response is used because it describes disease findings in tissue examined after pre-operative treatment and surgery. It is distinct from radiographic response, recurrence, and survival: a pCR result does not by itself establish what happens to participants over longer follow-up. The registry lists a 5 years timeframe, but does not give additional detail about how that timeframe applies to this post-surgery response assessment.

The posted arm results are 26.6% with a 95% confidence interval of 16.3% to 39.1% for chemoradiotherapy plus cetuximab, and 26.7% with a 95% confidence interval of 16.1% to 39.7% for chemoradiotherapy alone. The associated comparison is reported as a risk difference. These figures describe the observed pCR rates and the uncertainty around them; they do not establish that the regimens are equivalent or that a particular biological effect is absent.

7. Results Posted in the Registry

• Chemoradiotherapy Alone: 26.7% (16/60) versus 26.6% (17/64) on control; risk difference 0.1 percentage points (95% CI -15.5 to 15.7), risk ratio 1.00 (0.56–1.80); unadjusted two-proportion z-test p = 0.990.

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.

To Determine Objective Response Rate (ORR) Based on RECIST Local Recurrence-free Survival in These Patient Groups; Overall and Recurrence-free Survival in These Cohorts.

• 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:
  • Chemoradiotherapy Alone: 43.5% (27/62) versus 52.2% (35/67) on control; risk difference -8.7 percentage points (95% CI -25.9 to 8.5), risk ratio 0.83 (0.58–1.20); unadjusted two-proportion z-test p = 0.324.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Chemoradiotherapy Alone and the control. The interval gives the range of effects that remain compatible with the data.

KRAS Mutation Rate

• 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:
  • Chemoradiotherapy Alone: 44.1% (15/34) versus 32.5% (13/40) on control; risk difference 11.6 percentage points (95% CI -10.5 to 33.7), risk ratio 1.36 (0.76–2.44); unadjusted two-proportion z-test p = 0.304.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Chemoradiotherapy Alone and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies secondary questions involving objective response, local recurrence-free survival, overall survival, recurrence-free survival, and KRAS mutation rate. The posted result records include objective response rate and KRAS mutation rate; results for the other listed survival outcomes are not reported in the registry record. The available secondary endpoints address different aspects of response and disease course, and they should not be treated as interchangeable with the primary pathologic response endpoint.

The overall pattern in the posted secondary comparisons does not supply a clear, precise corroboration of the primary result. The secondary estimates are unadjusted, and their confidence intervals include values on both sides of no difference. This pattern is compatible with uncertainty rather than a definitive conclusion about whether the regimens differ. The secondary outcome records also use different denominators, which means their results concern different endpoint populations; the registry does not explain those differences.

Secondary endpoints often involve multiple questions. When many comparisons are examined, the chance of at least one apparently unusual result can increase, unless an appropriate multiplicity strategy is specified. No multiplicity adjustment or hierarchy among secondary outcomes is reported in the registry record. Consequently, unadjusted secondary p-values carry less weight than a prespecified primary comparison and should be regarded as descriptive rather than confirmatory. The registry also does not report analyses for the secondary endpoints in its analysis field.

The secondary results can provide context for the primary pCR finding, but they cannot substitute for missing survival results or resolve uncertainty in the primary comparison. In particular, response and mutation endpoints do not establish longer-term outcomes. The absence of posted results for listed survival measures should be treated as missing information, not as evidence that no events occurred or that the groups had the same survival experience.

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

• To Determine Objective Response Rate (ORR) Based on RECIST Local Recurrence-free Survival in These Patient Groups; Overall and Recurrence-free Survival in These Cohorts.
• 5- Year Overall Survival (OS) Rate
• Recurrence-free Survival (RFS) Rate at 5 Years
• KRAS Mutation Rate

9. Statistical Interpretation

10. Statistical Methods Explained

General: randomized comparisons. Random allocation is intended to make treatment groups comparable, on average, with respect to measured and unmeasured characteristics at the time of assignment. The registry identifies this trial as randomized and parallel, but does not report the randomization procedure, allocation concealment method, or stratification factors. Those implementation details are not reported in the registry record. Randomization supports a comparative interpretation, but it does not remove uncertainty caused by limited enrollment, missing outcomes, or differences that arise after assignment.

General: binary outcomes. The primary outcome is a binary event: each participant either meets the registry’s pCR definition or does not. A percentage summarizes the share meeting that definition in each group. The primary results report 26.6% among 64 participants and 26.7% among 60 participants. These rates are estimates from the endpoint populations, not guaranteed values for every similar population. The registry gives 95% confidence intervals for each rate to communicate sampling uncertainty.

General: risk difference. A risk difference expresses the absolute contrast between event rates in two groups. A value near zero indicates that the observed rates are close on that scale. The reported primary risk-difference estimate is 0.001, and its 95% confidence interval runs from -0.155 to 0.157. The interval includes zero and values in both directions. The registry’s contrast is not adjusted for other variables in the posted result. The unadjusted p-value is 0.99.

General: confidence intervals. A confidence interval is a range produced by a statistical method that reflects uncertainty in an estimate. In repeated use of the same method under its assumptions, intervals at the stated confidence level are designed to cover the target parameter at the stated rate. A 95% confidence interval is not a statement that there is a 95% probability that this particular fixed parameter lies within the observed interval. For this trial, the broad interval for the risk difference means that the data are compatible with a range of potentially important contrasts as well as a contrast near zero.

General: p-values. A p-value summarizes how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the statistical model. It is not an effect-size measure, does not show the probability that the null hypothesis is true, and does not measure clinical importance. The reported p-value is unadjusted. The registry does not describe the test used or a prespecified threshold in the trial’s own statistical plan.

General: masking and outcome assessment. The record lists no masking. Awareness of treatment assignment can influence care, reporting, or outcome assessment, depending on the outcome and how it is measured. Pathologic assessment uses tissue findings, but the registry does not specify who assessed the specimens, whether assessment was standardized, or whether assessors were masked. It would be inappropriate to assume those procedures from the endpoint definition alone.

General: over-dispersion. Over-dispersion occurs when the observed variability in data is greater than a model assumes. It is especially relevant in settings where outcomes are clustered or where variation differs across units. A simple binary response comparison does not itself establish whether over-dispersion was evaluated. The registry does not report a model specification or an assessment of over-dispersion, so no such adjustment can be attributed to the trial analysis.

General: planning calculations. The posted sample-size illustrations are based on the observed effect, two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. They examine planning for 100%, 75%, and 50% of the observed effect. These calculations are illustrations, not the trial’s original design justification. The original sample-size assumptions and the trial’s own power target are not reported in the registry record.

The registry lists no reported analyses for the secondary outcomes in its analysis field. The comparisons displayed for the posted outcomes are unadjusted, and no covariate-adjusted analysis, sensitivity analysis, interim analysis, or multiplicity procedure is described in the registry record. This absence of detail does not show that no such work was done; it means that the posted record does not document it. Statistical interpretation should therefore stay close to the estimates, intervals, denominators, and unadjusted comparisons that are actually recorded.

11. Confidence Intervals and Precision

Precision concerns how tightly an estimate is determined by the observed data. The primary arm-specific estimates have 95% confidence intervals of 16.3% to 39.1% for chemoradiotherapy plus cetuximab and 16.1% to 39.7% for chemoradiotherapy alone. Both intervals are broad in relation to their point estimates. This reflects considerable uncertainty about the response percentage in either group.

For the between-group contrast, the risk-difference estimate is 0.001 and the 95% confidence interval is -0.155 to 0.157. The interval includes zero and extends to values on both sides of it. Thus, the estimate is not precise enough to distinguish a near-zero contrast from a range of larger positive or negative contrasts. The unadjusted p-value of 0.99 is consistent with the small point estimate relative to the uncertainty, but the interval is more informative about the range of contrasts compatible with the data.

Arm-specific intervals and a comparison interval answer related but distinct questions. The former describe uncertainty in each group’s response percentage; the latter describes uncertainty in the difference between groups. Overlap between the arm-specific intervals is not itself a formal test of the treatment contrast. The direct risk-difference interval should be used for that purpose.

Confidence intervals depend on statistical assumptions and the data included in the analysis. The record identifies a post-surgery population but does not explain how participants without an evaluable outcome were handled. It also does not describe the precise interval method. These omissions matter when evaluating the scope of the uncertainty statement. The posted intervals are useful descriptions of statistical precision, but they cannot resolve uncertainty about endpoint availability, analysis procedures, or clinical importance.

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 participants per arm for 80% power and participants per arm for 90% power. They are not total event counts: the record’s planning assumptions specify that time-to-event calculations, if present, use total events, while other outcomes use participants per arm. The posted primary endpoint is a binary percentage outcome, so its planning figures are expressed per arm.

The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use the observed effect as a reference, with separate planning scenarios for 100%, 75%, and 50% of that observed effect. The 80% power column gives the estimated participants per arm under the stated assumptions for a design with 80% power to detect the specified effect. The 90% power column gives the corresponding per-arm planning figure for 90% power. Greater power means a higher chance of detecting the specified effect if that effect is present and the assumptions hold.

Smaller effects require more participants to detect under otherwise unchanged assumptions. The figures are therefore sensitive to which fraction of the observed effect is chosen; they should not be read as a fixed requirement independent of the target effect. The primary comparison’s observed risk-difference estimate is 0.001, so planning based on that observed contrast yields very large illustrative requirements. These calculations are not observed power. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

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 = 0.266; treatment proportion p₁ = 0.267; average p̄ = 0.266.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6250 = 1.2250.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6250 = 0.5260.
4. n = (1.2250 + 0.5260)² / (0.0010)² = 2,825,591.6, rounded up to 2,825,592 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 <- 0.265625                          # control proportion
p1 <- 0.266666666666667                          # 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(527111)
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 = 2,825,592 (80% power), 3,782,665 (90% power)
 75% of observed effect: n per arm = 5,021,709 (80% power), 6,722,642 (90% power)
 50% of observed effect: n per arm = 11,295,318 (80% power), 15,121,226 (90% power)
power.prop.test: 2825592 
Simulated power at n = 2,825,592 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. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary questions, including objective response, recurrence-related outcomes, overall survival, and KRAS mutation rate. Examining several outcomes can create a multiplicity problem: even when no true group differences exist, repeated testing can increase the chance of at least one apparently notable result. General approaches include prespecifying a primary comparison, adjusting significance thresholds, or setting an ordered testing strategy. The registry record does not report whether any such procedure was planned or used.

The posted secondary comparisons are unadjusted. Their p-values should therefore not be interpreted as if they were the sole analysis conducted. The record does not identify a statistical analysis plan, testing hierarchy, interim analyses, or other adjustments. It is also not possible to determine from the registry whether the listed outcome measures reflect all analyses that were performed.

Missing-data handling is another important uncertainty. The primary endpoint is defined for a post-surgery population, and its group denominators are 64 and 60, while total enrollment is 139. The registry does not explain why these populations differ or state whether participants without an evaluable pCR outcome were excluded, imputed, or handled through another approach. Reasons for differing denominators across posted endpoints are also not reported. No assumptions about missing outcomes should be inferred from the available counts.

The analysis population is therefore only partly described. The registry labels the primary population as post-surgery, but does not report whether the primary analysis followed intention-to-treat principles, how treatment changes were addressed, or how protocol deviations were handled. These details affect the interpretation of a randomized comparison because excluding participants after randomization can alter group comparability. The record’s lack of these details does not demonstrate a flaw in the analysis; it limits the ability to assess the analysis independently.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: dehydration (7.5%), diarrhea (7.5%), mucositis (3.2%), sepsis (3.0%), abdominal pain (1.6%).

The registry reports serious adverse events affecting 10 of 67 participants in the chemoradiotherapy-plus-cetuximab group and 5 of 62 participants in the chemoradiotherapy-alone group. The at-risk counts are the denominators recorded for these serious adverse event summaries. These counts describe the posted safety data; they do not by themselves show whether the difference between groups is statistically reliable or attributable to a particular regimen.

The listed top serious adverse event terms include DEHYDRATION (7.5%), DIARRHEA (7.5%), MUCOSITIS (3.2%), SEPSIS (3.0%), ABDOMINAL PAIN (1.6%), and ENTERITIS (1.6%). The record does not clearly assign these listed term percentages to a specific group in the information available, so they should not be interpreted as arm-specific rates. Serious adverse events are distinct from the broader other-adverse-event counts, which are reported as 61 of 67 and 47 of 62 in the respective groups.

Death counts are not reported in the registry record. The posted summaries do not provide event timing, severity grading details, exposure-adjusted rates, or a comparative safety analysis. These descriptive data should be read as counts and listed terms, not as a complete account of comparative safety.

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

The primary registry result describes similar observed pCR percentages in the two randomized groups, with a risk-difference estimate near zero. The 95% confidence interval for that difference is broad and includes values in both directions. The data therefore do not establish a precise treatment contrast. A near-zero point estimate should not be read as proof that the regimens are equivalent, and the wide interval should not be read as proof of a clinically important difference.

The result is specific to the registry’s pCR definition and post-surgery population. It does not directly answer whether the groups differed in survival, recurrence, symptoms, or other clinical outcomes. Although the registry lists survival-related secondary questions, their results are not reported in the posted endpoint records. A pathologic response finding is one outcome among several relevant to understanding a trial; it cannot stand in for outcomes that are not available.

The p-value of 0.99 does not show that the probability of benefit is zero, and it does not establish that the observed rates are identical in the populations from which the participants came. It summarizes the unadjusted comparison under a statistical null model. The confidence interval is essential because it conveys the range of contrasts that remain compatible with the data and makes the imprecision visible.

Interpretation is further limited by incomplete information about the original design assumptions, analysis plan, missing outcomes, and endpoint assessment procedures. The posted comparison remains useful as a description of what was recorded, but it should be understood alongside those limitations. No treatment recommendation follows from these registry data alone.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between a small point estimate and a precise estimate. The primary risk-difference estimate is 0.001, while its 95% confidence interval ranges from -0.155 to 0.157. The point estimate is close to zero, but the interval shows that the data do not sharply determine the size or direction of the underlying contrast. Reading only the point estimate would understate uncertainty; reading only the p-value would obscure the range of plausible effects.

The record also highlights the importance of distinguishing endpoint populations. The trial enrolled 139 participants, while the primary endpoint is reported for the post-surgery population with group denominators of 64 and 60. Without an explanation of how these populations relate, readers cannot fully assess the role of missing or unevaluable outcomes. Explicit reporting of analysis populations and missing-data methods is central to interpreting randomized trials.

The secondary findings raise a related issue: several outcomes may be examined, yet the record does not describe a multiplicity strategy or provide posted analyses for every listed outcome. An unadjusted result is not automatically confirmatory when multiple questions are under consideration. The sample-size illustrations further demonstrate that planning requirements depend strongly on the effect a study is intended to detect, and those illustrations do not reveal the assumptions used to design the original trial.

Together, these features make the registry useful for statistical reading: it offers group estimates and uncertainty, while also leaving key design and analysis details unresolved. Careful interpretation distinguishes what the data estimate from what the record does not document.

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

Several trial-specific limitations affect interpretation. The primary outcome is reported in a post-surgery population, but the registry does not explain how the endpoint denominators relate to enrollment of 139 or how participants without an evaluable pathology result were handled. This prevents a full assessment of missing-outcome effects and of how closely the analysis population reflects the randomized groups.

The registry marks the trial as unmasked but does not describe the pathology assessment process or whether assessors were unaware of treatment assignment. The endpoint uses a defined tissue-based criterion, but the record does not give information about central review, consistency across assessors, or other quality-control procedures. Those details should not be assumed.

The primary comparison is imprecise: its 95% confidence interval includes contrasts in both directions. The registry does not report a prespecified equivalence or non-inferiority framework, so the small observed contrast cannot be used to conclude that the regimens are equivalent. The record also does not report the original sample-size rationale, planned statistical model, interim analyses, or a detailed analysis plan.

Some listed secondary outcomes do not have posted results, and no multiplicity approach is described. The safety information is limited to event counts and listed terms; the registry does not report death counts or a complete comparative safety analysis. Reasons for differing denominators across outcomes are not reported. These limitations concern what can be established from the registry record and do not, by themselves, demonstrate how the trial was conducted beyond the details it records.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Pre-op Rectal ChemoRad +/- Cetuximab — NCT00527111.
• Registry record last updated 2016-11-03; status last verified 2016-09.
• Results first posted 2016-11-03.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed randomized Phase II parallel-group trial sponsored by US Oncology Research, with enrollment of 139 participants. It compared pre-operative pelvic irradiation and 5-fluorouracil with versus without cetuximab in locally advanced adenocarcinoma of the rectum. The trial was unmasked.

The primary endpoint was the percentage with pathologic complete response in the post-surgery population. The reported percentages were 26.6% with cetuximab and 26.7% without it; the risk-difference estimate was 0.001, with a 95% confidence interval from -0.155 to 0.157 and an unadjusted p-value of 0.99. The interval indicates substantial uncertainty around the contrast.

Posted secondary results include objective response rate and KRAS mutation rate. Other listed survival outcomes do not have posted results in the registry record. The record does not report the original sample-size justification, detailed analysis plan, multiplicity procedure, or handling of missing outcomes.