Study Comparing Whole Breast Radiotherapy With a Daily Versus a Weekly Tumor: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study Comparing Whole Breast Radiotherapy With a Daily Versus a Weekly Tumor (NCT01000662), a randomized phase 3 study. The primary outcome is Number of Participants With Acute Radiation Toxicities Recorded According to Radiation Therapy Oncology Group (RTOG).

2. Clinical Question

3. Trial Design

This is a Phase III randomized, double-masked, parallel-group study. The registry lists enrollment of 412 and a completed status. The listed study start is 2009-03, with primary completion in 2012-07. The endpoint arm denominators are 202 for the daily boost group and 198 for the weekly boost group. The reasons for any difference between overall enrollment and the endpoint denominators are not reported in the registry record.

Both groups received prone whole-breast radiotherapy described as an accelerated three week regimen. The randomized contrast was the timing of the tumor-bed boost: daily in one arm and weekly in the other. The summary specifies that the weekly boost was delivered on Friday before the weekend break. It does not describe additional treatment differences between arms.

The record identifies random allocation, double masking, and a parallel model, but does not report how the random sequence was generated, how allocation was concealed, or who was masked. The planned allocation ratio is not reported in the registry record. The number enrolled is not the same as an endpoint-specific analysis population unless the record establishes that relationship; the method used to define or retain participants for the primary comparison is not described.

The stated study aim is to test whether the weekly boost is as well tolerated as the daily boost during accelerated prone radiotherapy. The primary outcome is a count of participants with grade 2 or greater acute radiation toxicity at Day 60. The registry also lists quality-of-life and pain outcomes. Details of the original protocol, including the trial's own sample-size justification and analysis plan, 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: Patients receiving either daily or weekly boost to radiation therapy

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Acute Radiation Toxicities Recorded According to Radiation Therapy Oncology Group (RTOG), measured over Day 60.

The primary endpoint is the number of participants with acute radiation toxicities recorded according to RTOG at Day 60. The endpoint description specifies grade 2 or greater toxicity after three weeks of whole-breast IMRT, comparing the weekly boost with the daily boost. It also describes a scale ranging from no symptoms to death directly related to radiation effects, but the reported primary measure is the number of participants meeting the stated grade threshold, not a mean toxicity score.

This count is aligned with the registry summary's tolerability question: it records how many participants in each arm experienced a qualifying acute toxicity by the stated follow-up time. A count is straightforward to interpret as an event occurrence, but it does not convey the severity distribution above the threshold, the timing of each event, or the duration of symptoms. Those details are not reported in the registry record.

The posted arm counts are 22 participants in the daily boost group and 16 in the weekly boost group. The comparison is therefore about the frequency of the defined event in the two randomized groups, rather than a comparison of average toxicity grades. The record does not give additional rationale for choosing this particular endpoint or explain whether it was the sole primary endpoint in the original protocol.

7. Results Posted in the Registry

• ARM 2 Weekly Boost: 8.1% (16/198) versus 10.9% (22/202) on control; risk difference -2.8 percentage points (95% CI -8.5 to 2.9), risk ratio 0.74 (0.40–1.37); unadjusted two-proportion z-test p = 0.338.

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.

Average Score on Brief Pain Inventory (BPI) Scale

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • ARM 2 Weekly Boost: mean 1.71 versus 1.46 on control; difference 0.25 (95% CI -0.07 to 0.57), standardized effect d = 0.15; z-test p = 0.123.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ARM 2 Weekly Boost and the control. The interval gives the range of effects that remain compatible with the data.

Average Score on Brief Pain Inventory (BPI)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • ARM 2 Weekly Boost: mean 1.66 versus 1.46 on control; difference 0.20 (95% CI -0.12 to 0.52), standardized effect d = 0.12; z-test p = 0.220.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between ARM 2 Weekly Boost and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists several secondary outcomes, including pain, breast cancer treatment outcomes, vitality, and breast quality of life. The posted secondary comparative summaries in the record concern the Brief Pain Inventory at baseline and at the end of treatment. Results for the other listed secondary outcomes are not reported in the registry record.

Across the posted secondary comparisons, the estimated mean differences are positive, while the posted intervals include zero and the unadjusted p-values are 0.123 at baseline and 0.22 at the end of treatment. The record therefore does not present a clear, precise secondary comparison that changes the interpretation of the primary toxicity result. These outcomes measure different aspects of participants' reported experience from the primary count of acute radiation toxicities, so they are complementary rather than interchangeable evidence.

Secondary results are often useful for describing whether a primary outcome is accompanied by changes in other domains. Their evidential weight depends on the prespecified role of each outcome, the completeness of its results, and the analysis plan. Those details are not reported in the registry record. The registry lists 13 outcome measures, and the posted summaries do not provide a full set of comparative results for all listed outcomes.

Multiplicity is also relevant: when many outcomes are examined, some may appear notable by chance even if there are no underlying differences. The record does not describe whether secondary analyses were adjusted for multiple testing or designated as exploratory. For that reason, unadjusted secondary findings should be treated as descriptive and interpreted cautiously. They should not be used to overturn or replace the primary endpoint result, and absence of a posted result for a listed outcome should not be interpreted as evidence of no difference.

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

• Average Score on Breast Cancer Treatment Outcomes Scale (BCTOS) at Baseline
• Score on "SF-36 v2 Vitality" Scale
• Average Score on Brief Pain Inventory (BPI) Scale
• Average Score on Radiation Therapy Oncology Group (RTOG) Breast Quality of Life Scale
• Average Score on Breast Cancer Treatment Outcomes Scale (BCTOS) at the End of Treatment
• Average Score on Breast Cancer Treatment Outcomes Scale (BCTOS)
• Score on "SF-36 v2 Vitality" Scale
• Score on "SF-36 v2 Vitality" Scale 45-60 Days After Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary comparison concerns a binary event: whether a participant had a grade 2 or greater acute radiation toxicity recorded by Day 60. The registry reports arm-specific event counts and denominators, then presents comparative measures. The details of the statistical procedures used to produce those comparisons are not reported in the registry record. The explanations below describe the meaning of the measures in general and distinguish them from unreported analysis details.

What does the risk difference describe?

In general, a risk difference is the difference between the event proportions in two groups. Its sign depends on the order of comparison. In the posted comparison, the weekly boost arm is compared with the daily boost arm. A negative estimate therefore indicates a lower observed event proportion in the weekly arm; it does not, by itself, establish that the difference is real or important. The registry's arm counts are 16 of 198 for weekly boost and 22 of 202 for daily boost. The posted risk difference is negative, and its confidence interval extends across zero.

The risk difference is expressed on an absolute scale, which can make it useful for describing how much event frequency separates the groups. The interval communicates uncertainty around that estimate. Since the interval includes values on both sides of zero, the posted data do not sharply distinguish a reduction from an increase in event frequency. The registry does not specify the confidence level or calculation method for this interval.

How do the relative measures differ?

The relative risk compares event proportions as a ratio, while the odds ratio compares event odds as a ratio. Both describe the direction and relative scale of the contrast, but neither is an absolute difference. The registry posts a relative risk estimate of 0.742 and an odds ratio estimate of 0.719. The intervals posted for these measures include the ratio value that corresponds to no group difference. Because each scale has different interpretation, relative estimates should be read alongside the arm counts and the absolute risk difference rather than in isolation.

In general, a ratio below the no-difference value indicates a lower event frequency or odds in the first-named group, depending on the measure and comparison order. It is not a probability that the treatment works, and it does not state how many participants are affected. Relative and absolute measures can give different impressions when event frequencies are not large, so both the scale and the underlying endpoint matter.

What does the p-value say?

The registry posts an unadjusted p-value of 0.338 for the primary comparison. In general, a p-value describes the probability, under a specified null model and its assumptions, of obtaining results at least as discrepant from that model as those observed. It is not the probability that the null hypothesis is true, and it is not a measure of clinical importance. The record does not identify the test used, its assumptions, or whether any adjustments were part of the original analysis.

The word unadjusted matters because the p-value is not identified as corrected for testing multiple outcomes or comparisons. The registry record does not describe a multiplicity plan. The reported p-value should therefore not be treated as a complete account of how the trial controlled error across its outcome set.

What is not specified about the analysis?

The registry does not report a detailed statistical analysis plan, the original protocol's analysis populations, or the handling of missing endpoint data. It also does not report a formal analysis method for the primary comparison or identify whether covariate adjustment was planned. The reported arm summaries can be described, but these missing details prevent a full assessment of whether the posted comparison follows a prespecified analysis.

The primary outcome is a participant count, not a time-to-event measure. No event-time analysis is reported for it. In general, the distinction matters: a count of participants meeting a definition by a set assessment time does not use the same information as an analysis of the timing of events. The registry's stated Day 60 time point defines the observation window for the primary endpoint, while later events or follow-up are not described in this result.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate the comparison, not whether the observed estimate is important or whether an intervention should be used. For the primary risk difference, the posted interval extends from a negative value to a positive value and includes zero. This means the data are compatible with a range of possible group differences, including a reduction or an increase in the qualifying event frequency in the weekly arm. The interval does not pinpoint the direction of the underlying difference.

The primary arm counts are 22 of 202 for daily boost and 16 of 198 for weekly boost. The point estimate is negative for weekly compared with daily, but the interval is broad enough to include the no-difference value. The unadjusted p-value of 0.338 is consistent with that uncertainty; it does not settle the question of equivalence. The registry does not report the confidence level or method used to construct the interval, so its exact coverage interpretation cannot be confirmed from the record.

Confidence intervals are useful because they show uncertainty on the same scale as the effect estimate. In general, a narrower interval indicates greater precision, while a wider interval leaves more plausible values compatible with the data. Precision depends on factors such as the number of observed participants and events, variability, and the analysis method. The posted result alone does not reveal how those factors were handled beyond the arm counts and comparison summaries.

The relative-measure intervals also include their no-difference value. Taken together, the estimates do not provide a precise answer about the size or direction of a possible difference. This is uncertainty, not evidence that the arms are identical. A formal equivalence or noninferiority conclusion would require a prespecified margin and appropriate analysis, which 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 participants per arm for this binary endpoint. They are not total events. The sample-size assumptions listed for these illustrations 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. The trial's own original sample-size assumptions and justification are not reported in the registry record.

For example, planning for 100% of the observed effect gives 1,706 participants per arm for 80% power and 2,283 participants per arm for 90% power. Planning for 75% of the observed effect gives 3,133 participants per arm for 80% power and 4,194 participants per arm for 90% power. The smaller target effect therefore requires more participants per arm under the stated assumptions. The same direction applies across the listed planning scenarios: detecting a smaller difference generally requires more information.

In general, power is the probability that a study will detect an effect of a specified size under the assumptions used for planning, if that effect is present. The 80% and 90% columns represent two different target probabilities of detecting the assumed effect, not confidence levels and not guarantees about a future result. A higher target probability generally requires a larger planned sample for a given effect and assumptions.

These figures are planning illustrations based on the observed effect, not observed power. They should not be read as the original trial's planned enrollment target or as evidence that the completed study had a particular probability of success. Time-to-event planning displays use total event counts, but the figures for this binary endpoint are participants per arm.

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 = 0.109; treatment proportion p₁ = 0.081; average p̄ = 0.095.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4144 = 0.8122.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4139 = 0.3484.
4. n = (0.8122 + 0.3484)² / (-0.0281)² = 1,705.4, rounded up to 1,706 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 <- 0.108910891089109                          # control proportion
p1 <- 0.0808080808080808                          # 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(1000662)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 1,706 (80% power), 2,283 (90% power)
 75% of observed effect: n per arm = 3,133 (80% power), 4,194 (90% power)
 50% of observed effect: n per arm = 7,274 (80% power), 9,738 (90% power)
power.prop.test: 1705.4 
Simulated power at n = 1,706 per arm: 0.805 (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 multiple secondary outcomes, but does not report a statistical analysis plan describing how those outcomes were prioritized or analyzed. It does not report whether the primary endpoint was the only primary outcome in the original protocol, whether secondary outcomes were prespecified in their posted form, or whether a hierarchy of testing was used. The number of reported analyses is listed as zero, and no reported analyses are included in the registry record.

In general, testing multiple outcomes increases the chance that at least one result may appear statistically noteworthy by chance. Methods such as a prespecified hierarchy or multiplicity adjustment can address that issue, but the registry does not state that any such method was used. The primary p-value is identified as unadjusted, and the secondary p-values are also presented as unadjusted. Without a stated plan, the results cannot be interpreted as controlling an overall error rate across all endpoints.

Missing-data methods are not reported in the registry record. The record does not say how missing Day 60 assessments were handled, whether participants with incomplete follow-up were included in the primary comparison, or whether any sensitivity analyses were conducted. The endpoint denominators are listed by arm, but the reason participants may not appear in those denominators is not described. No assumptions about missing outcomes can therefore be assessed.

The record also does not describe the analysis population—for example, whether the primary comparison followed the randomized assignment for every participant or used another population definition. It does not report whether protocol deviations, treatment adherence, or crossovers were considered. These are important details because the chosen population and missing-data assumptions can affect a comparison, even when the arm counts and summary estimates are clear.

These omissions do not invalidate the posted summaries, but they limit assessment of how robustly the analysis answers the stated trial question. The registry record does not include enough information to determine whether multiplicity, missingness, or analysis-population choices were addressed in the original statistical plan.

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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero participants with serious adverse events in each arm: the serious-event denominator is 202 for daily boost and 198 for weekly boost. It also reports participants with other adverse events: 89 in the daily arm and 72 in the weekly arm, using the same respective denominators. These are participant counts, not counts of all separate event episodes. The record does not provide serious adverse event terms in its listed top terms.

The posted serious-event counts should be read as registry entries for the recorded categories, not as proof that no serious events occurred beyond the record's observation or reporting process. The death fields are not reported in the registry record, and adverse-event definitions, collection methods, and follow-up duration are not described in detail. No conclusions about comparative safety should be drawn from these counts alone; they are descriptive summaries that require the stated categories and reporting context.

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

The primary result describes the number of participants with a grade 2 or greater acute radiation toxicity recorded at Day 60. The observed count is lower in the weekly boost arm than in the daily boost arm, and the posted risk difference points in that direction. However, its confidence interval spans zero and the unadjusted p-value is 0.338. The result therefore leaves substantial uncertainty about the direction and size of a true difference.

The registry summary states that the study intended to test whether the weekly boost was as well tolerated as the daily boost. A nonsignificant comparison does not establish that the schedules are equivalent. Equivalence or noninferiority requires a prespecified margin that defines the largest acceptable difference, along with a design and analysis suited to that question. Such a margin and analysis plan are not reported in the registry record.

The result also does not show that the schedules are identical, or that one schedule is better. The posted counts represent this endpoint at the specified assessment time; they do not describe every possible toxicity, the full range of toxicity grades, or outcomes beyond Day 60. Quality-of-life and pain outcomes address different dimensions, and the available secondary summaries do not replace the primary comparison.

These findings are statistical descriptions of the posted trial results, not medical advice. They do not determine what treatment is appropriate for any individual. Interpretation should remain bounded by the population, intervention schedules, endpoint definition, follow-up time, and analysis information recorded for this study. Several protocol and analysis details needed for a fuller assessment are not reported in the registry record.

17. Why This Trial Matters Statistically

This trial illustrates why the wording of a clinical question matters. The study summary frames the comparison as whether a weekly boost is as well tolerated as a daily boost, while the primary result is a conventional between-group comparison of event counts. Those are related ideas, but a failure to detect a difference is not the same as demonstrating comparable tolerability within a clinically acceptable margin. The latter requires a clearly stated margin and a design that directly evaluates it.

It also demonstrates the value of reading an effect estimate with its uncertainty rather than relying on a p-value alone. The observed count pattern and negative risk difference point toward fewer qualifying events in the weekly arm, but the interval includes both sides of no difference. The posted estimate therefore carries more nuance than a simple statement that the groups were or were not statistically different.

The registry's secondary outcome list highlights another statistical issue: a trial can collect several domains, but the evidence from each depends on prespecification, completeness, and multiplicity handling. The record lists a range of patient-reported outcomes, while the posted summaries cover only some of them. Without the full analysis plan and outcome results, it is difficult to assess the overall pattern comprehensively.

Finally, the planning illustrations make clear that sample-size needs depend on the effect size a future study seeks to detect. Smaller target effects require more participants per arm under the stated planning assumptions. These illustrations are not the original design justification and are not a measure of the completed study's observed power. Taken together, these points show how endpoint definition, precision, design intent, and reporting completeness shape statistical interpretation.

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.

Several limitations are specific to the registry record. It defines the primary endpoint by a grade threshold at Day 60, but does not report the distribution of toxicity grades, event timing, duration, or detailed ascertainment procedures. The result therefore cannot describe the full experience of acute toxicity or later outcomes.

The record lists overall enrollment of 412 and endpoint denominators of 202 and 198 by arm, but does not explain how the endpoint populations were formed or how participants absent from those denominators were handled. Missing-data methods, analysis populations, protocol deviations, and adherence information are not reported in the registry record. These omissions limit assessment of potential bias in the primary comparison.

The design is identified as randomized, double-masked, and parallel, but implementation details are not given. The record does not describe sequence generation, allocation concealment, or who was masked. It also does not report the original sample-size justification, a noninferiority or equivalence margin, the formal analysis method, or a multiplicity plan. Consequently, the posted comparison cannot be fully checked against the original trial objectives and prespecified methods.

The registry lists multiple secondary outcomes, but comparative summaries are not present for all of them. The available secondary results are unadjusted, and the record does not clarify whether they were planned as confirmatory or exploratory. Serious adverse event terms are not listed, and death counts are not reported in the registry record. These reporting gaps do not determine what the unreported results would show, but they restrict conclusions about the wider outcome and safety profile.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study Comparing Whole Breast Radiotherapy With a Daily Versus a Weekly Tumor — NCT01000662.
• Registry record last updated 2020-08-06; status last verified 2020-07.
• Results first posted 2015-05-29.
• 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 Phase III randomized, double-masked, parallel study comparing daily with weekly tumor-bed boosts during accelerated prone whole-breast radiotherapy for patients with Stages 0-II breast cancer. Overall enrollment is 412. The primary outcome is the number of participants with grade 2 or greater acute radiation toxicity at Day 60.

The posted primary counts are 22 of 202 participants in the daily boost arm and 16 of 198 in the weekly boost arm. The comparative estimate points toward fewer qualifying events in the weekly arm, but its interval spans zero and the unadjusted p-value is 0.338. The record does not report the original analysis plan, missing-data handling, multiplicity approach, or a margin for an equivalence or noninferiority conclusion. Secondary and adverse-event summaries add context but do not resolve those limitations.