Higher Per Daily Treatment-Dose Radiation Therapy or Standard Per Daily Treatment Radiation Therapy in Treating Patients With Early-Stage Breast Cancer That Was Removed by Surgery: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Higher Per Daily Treatment-Dose Radiation Therapy or Standard Per Daily Treatment Radiation Therapy in Treating Patients With Early-Stage Breast Cancer That Was Removed by Surgery (NCT01349322), a randomized phase 3 study. The primary outcome is Percentage of Participants With In-breast Recurrence (Local Failure).

2. Clinical Question

The clinical contrast is between treatment schedules and boost timing, not between radiation and no radiation. In the accelerated approach, the boost is concurrent with hypofractionated whole-breast treatment; in the comparator, the boost follows standard-fractionation whole-breast treatment. The primary endpoint is a local recurrence in the treated breast, including events within or outside the treatment field and invasive or non-invasive recurrence.

The primary result is expressed as a five-year cumulative incidence, with follow-up extending from randomization to last follow-up. Death without in-breast recurrence is treated as a competing event in the endpoint definition. The registry also reports a Cox-model hazard ratio and a non-inferiority analysis. Those time-to-event results address a different statistical summary from a simple comparison of the two five-year percentages.

The question is therefore not answered by the percentages alone. Interpretation also depends on the time-to-event analysis, its uncertainty, and the trial's non-inferiority framework. The margin and the detailed decision rules are not reported in the registry record, so the posted information does not support reconstructing that framework independently.

3. Trial Design

This is a randomized phase III trial with a parallel-group design and no masking. The registry lists enrollment of 2354 participants and identifies the Radiation Therapy Oncology Group as sponsor. The trial concerns breast cancer after surgery and compares two whole-breast radiation strategies with different fractionation and boost schedules.

One arm received standard-fractionation whole-breast irradiation with a sequential boost. The other received hypofractionated whole-breast irradiation with a concurrent boost. Because both the fractionation schedule and the timing of the boost differ, the contrast is between the treatment strategies as a whole. The record does not permit separating the contribution of fractionation from the contribution of boost timing.

The listed start date is 2011-05-24, and primary completion is recorded as 2022-01-25. The status is active, not recruiting. The maximum follow-up at the time of analysis was 10.1 years, while the primary and listed survival outcomes report five-year rates. The registry describes follow-up assessments during radiation treatment, after treatment, and annually; the detailed primary-endpoint schedule is stated in its outcome description.

Randomization supports comparison of assigned strategies, but the registry record does not report details such as the randomization sequence, allocation concealment, stratification factors, adherence, treatment crossovers, or the primary analysis population. Masking is recorded as NONE. This is relevant context for outcomes that might be assessed subjectively, although it does not by itself establish the presence or direction of bias.

The record lists 12 outcome measures, including survival, disease outcomes, adverse events, cosmetic outcomes, and translational research. Nine secondary outcomes are posted. The registry does not report the original sample-size justification or enough detail to reconstruct all aspects of the prespecified analysis plan.

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: Eligible 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: Eligible population

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With In-breast Recurrence (Local Failure), measured over From randomization to last follow-up. Evaluated weekly during radiation therapy (RT), last day of RT, 1, 6, and 12 months after RT completion, then annually. Maximum follow-up at time of analysis was 10.1 years. Five-year rates are reported here..

The primary endpoint is the percentage of participants with in-breast recurrence, also called local failure. A recurrence can be invasive or non-invasive and can occur within or outside the treatment field in the ipsilateral breast. The endpoint is time from randomization to the first qualifying recurrence. Participants without a recorded recurrence are followed to last known follow-up, and death without recurrence is treated as a competing risk.

This endpoint is relevant to the trial because it measures recurrence in the breast treated by the radiation strategies under comparison. It focuses on local control rather than survival or distant spread, which are reported as separate outcomes. The registry reports five-year cumulative-incidence rates, estimated with the cumulative incidence method. That method is appropriate to the stated competing-risk definition because a death without recurrence prevents a later observation of in-breast recurrence.

The record also says treatment comparisons are based on cause-specific hazards and that distributions of failure times are compared between arms. These analyses use the timing of events, rather than only whether an event was recorded by a fixed point. A five-year percentage and a hazard ratio therefore convey related but not identical information: one describes estimated cumulative incidence at a specified time, while the other summarizes the relative event hazard over follow-up under the model.

The endpoint's assessment schedule and the maximum follow-up are stated in the registry, but the registry record does not report all operational details of endpoint review or adjudication.

7. Results Posted in the Registry

• Hypofractionated Whole Breast Irradiation + Concurrent Boost (Arm 2): 1.9% (22/1138) versus 2.0% (22/1124) on control; risk difference -0.0 percentage points (95% CI -1.2 to 1.1), risk ratio 0.99 (0.55–1.77); unadjusted two-proportion z-test p = 0.967.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants Alive

• 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:
  • Hypofractionated Whole Breast Irradiation + Concurrent Boost: 95.1% (1082/1138) versus 95.7% (1076/1124) on control; risk difference -0.7 percentage points (95% CI -2.4 to 1.1), risk ratio 0.99 (0.98–1.01); unadjusted two-proportion z-test p = 0.460.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Hypofractionated Whole Breast Irradiation + Concurrent Boost and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Alive Without Disease

• 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:
  • Hypofractionated Whole Breast Irradiation + Concurrent Boost: 88.5% (1007/1138) versus 90.2% (1014/1124) on control; risk difference -1.7 percentage points (95% CI -4.3 to 0.8), risk ratio 0.98 (0.95–1.01); unadjusted two-proportion z-test p = 0.184.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Hypofractionated Whole Breast Irradiation + Concurrent Boost and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants Alive Without Distant Disease

• 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:
  • Hypofractionated Whole Breast Irradiation + Concurrent Boost: 90.2% (1026/1138) versus 91.5% (1028/1124) on control; risk difference -1.3 percentage points (95% CI -3.7 to 1.1), risk ratio 0.99 (0.96–1.01); unadjusted two-proportion z-test p = 0.284.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Hypofractionated Whole Breast Irradiation + Concurrent Boost and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover survival, disease-free and distant-disease-free status, adverse events, cosmetic assessments, and translational research. Nine secondary outcomes are posted out of 12 outcome measures listed in the registry. The three posted time-to-event outcomes show a broadly similar pattern in the arm-level estimates, with the comparator estimates numerically higher. Their tests do not establish a difference merely because the point estimates are not identical.

These outcomes add context to the primary local-recurrence result by addressing broader outcomes than recurrence in the treated breast. Survival and disease outcomes reflect different event definitions and can have different precision and clinical interpretations. Cosmetic and adverse-event outcomes address other aspects of treatment, while the listed dose-volume and genetic analyses concern associations or translational questions. They should not be treated as substitutes for the primary endpoint.

The registry reports superiority-type log-rank tests for the posted survival outcomes. Those tests answer whether the observed event-time patterns are inconsistent with a no-difference null under the test assumptions; they do not establish equivalence or non-inferiority. The registry does not report a multiplicity adjustment or a hierarchy of secondary hypotheses. When multiple outcomes are tested, unadjusted results carry less weight because the chance of at least one apparently notable result can rise across a collection of tests.

Secondary findings are therefore best viewed as supportive context, not as a set of separate definitive conclusions. Results not posted among the listed secondary outcomes are not reported in the registry record, and the record does not provide enough information to infer their direction or statistical significance.

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

• Percentage of Participants Alive
• Percentage of Participants Alive Without Disease
• Percentage of Participants Alive Without Distant Disease
• Number of Participants by Highest Grade Adverse Event Reported as Definitely, Probably, or Possibly Related to Protocol Treatment
• Change in Breast Cancer Treatment Outcome Scale (BCTOS) Cosmesis Subscale Score From Baseline to 3 Years
• Percentage of Participants With a Physician-reported Cosmetic Score of Excellent or Good at 3 Years
• Correlation Between Dose-volume Data and Both Adverse Events and Efficacy
• Translational Research of Single Nucleotide Polymorphisms (SNPs) in Transforming Growth Factor Beta 1 (TGFB1) and Ataxia-Telangiesctasia Mutated (ATM) Genes

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome combines an event definition, a follow-up period, and a statistical method. Keeping these components distinct helps prevent the five-year rates, the re-calculated risk difference, and the sponsor's hazard-ratio analysis from being treated as interchangeable.

What does the cumulative incidence estimate describe?

The cumulative incidence method estimates the probability of experiencing the event of interest by a specified time while accounting for a competing event. For this endpoint, the event of interest is in-breast recurrence and death without recurrence is the competing event. A competing event matters because a participant who dies without recurrence can no longer experience a later recurrence. Treating that death as though it were ordinary loss to follow-up could misrepresent the event probability.

The registry reports five-year cumulative-incidence estimates for the two arms. These are time-specific estimates, not simple counts divided by the number assigned to each arm. Follow-up can vary, and the method uses the recorded event and follow-up times. The arm-level 95% confidence intervals express uncertainty in each estimated rate.

Why are cause-specific hazards also reported?

A cause-specific hazard describes the instantaneous rate of the event of interest among participants who remain at risk, under the time-to-event model. The registry says comparisons are based on cause-specific hazards and reports a Cox regression hazard ratio. A hazard ratio summarizes the modeled relative event hazard between arms over follow-up. It is not a ratio of the five-year percentages, nor does it directly give an absolute difference in recurrence probability.

The Cox model uses event timing and the risk sets formed during follow-up. Its interpretation relies on the model's assumptions, including the proportional-hazards structure for a single summary hazard ratio. The registry record does not report diagnostics or further details that would allow those assumptions to be assessed from the posted summary alone. The stated protocol comparison of failure-time distributions is also not fully described in the registry record beyond the reported analysis.

What does the unadjusted re-calculation test?

The re-calculated risk difference and p-value use posted summary statistics for a simple, unadjusted comparison of the two arm-level percentages. They do not account for event timing in the same way as the cumulative-incidence and Cox analyses. They are useful as a transparent check on the posted percentages, but they are not a substitute for the sponsor's prespecified time-to-event analysis. Because the record flags a discrepancy, the sponsor's own analysis takes precedence.

A p-value measures how incompatible the observed data are with a specified null model, subject to the test's assumptions. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. A non-significant result in a conventional superiority test would not establish equivalence. Non-inferiority requires a prespecified margin and a decision rule; those details are not reported in the registry record.

Why do confidence intervals matter?

A confidence interval gives a range of effect estimates compatible with the data and analysis procedure at the stated confidence level. A narrow interval indicates greater precision than a wide interval, while the location of the interval indicates which effect values remain plausible. The 95% intervals around arm-level rates and the 90% interval around the sponsor-reported hazard ratio describe uncertainty for different quantities and use different confidence levels.

The sponsor's hazard-ratio interval includes values on either side of 1.00, so the posted interval allows a range of relative effects. It should not be recast as proof of no effect. For a non-inferiority question, the interval's relation to the prespecified margin is central, but that margin is not reported in the registry record. Without it, readers cannot independently apply the trial's non-inferiority criterion.

How should the secondary tests be read?

The registry reports log-rank tests for the posted survival outcomes. A log-rank test compares event-time distributions between groups under its assumptions; it does not by itself give the size of an effect. The registry does not report a single multiplicity-adjusted interpretation for the family of secondary outcomes. When many outcomes are examined, unadjusted p-values should be treated as exploratory or supportive rather than as a set of independent confirmatory findings.

General statistical principles explain why these methods differ; the registry record does not report every model specification, diagnostic, missing-data procedure, or analysis-population definition needed to reproduce the analyses in full.

11. Confidence Intervals and Precision

The arm-level recurrence estimates are 2.0% and 1.9%, with 95% confidence intervals of 1.4% to 2.9% and 1.3% to 2.7%. Each interval shows uncertainty in its own arm's estimated five-year cumulative incidence. The intervals overlap, but this does not itself quantify the uncertainty in the between-arm contrast or demonstrate equivalence.

The unadjusted re-calculated risk difference is -< 0.001, with a 95% confidence interval from -0.012 to 0.011. The interval spans values on either side of zero, meaning the simple comparison is compatible with more than one direction of difference. Its width is important: the point estimate is close to zero, but the interval does not restrict the effect to a single precise value. This calculation is distinct from the sponsor's time-to-event analysis.

The sponsor-reported hazard ratio is 1.32, and its 90% confidence interval runs from 0.84 to 2.05. This interval is broad relative to the point estimate and includes a range of possible relative hazards. Since it is a 90% interval rather than a 95% interval, it should not be directly compared with the arm-level 95% intervals as though they represented the same quantity and confidence level. The margin needed to judge non-inferiority is not reported in the registry record.

Confidence intervals describe statistical uncertainty under the relevant analysis; they do not capture every source of uncertainty, such as incomplete reporting or limitations in model assumptions. The registry provides a maximum follow-up of 10.1 years, but the primary result under discussion is the five-year rate. Precision at that time point does not establish what an estimate would be at a later time.

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 illustrations are based on the observed effect, not the trial's original design. For these percentage-based outcomes, the figures are participants per arm, rather than total events. The registry's stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm needed for an analysis to have an 80% chance of rejecting its null hypothesis if the assumed effect and other planning conditions hold. The 90% power column gives the corresponding illustration for a 90% chance. These are planning quantities, not guarantees about a future study, and they depend on the effect size and assumptions used in the calculation.

Rows describing planning for 75% or 50% of the observed effect assume a smaller effect than the row using 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm. The figures should be read as hypothetical planning scenarios under stated assumptions, not as a retrospective evaluation of whether this trial had enough participants.

This is not observed power. It is a prospective planning illustration derived from the observed estimate, and it does not describe the probability that the completed trial's result is correct. For any time-to-event illustration explicitly based on a Schoenfeld calculation, the stated unit would instead be total events; that is distinct from the participants-per-arm figures for percentage-based outcomes.

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 = 0.020; treatment proportion p₁ = 0.019; average p̄ = 0.019.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.1953 = 0.3828.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.1953 = 0.1644.
4. n = (0.3828 + 0.1644)² / (-0.0002)² = 5,164,147.1, rounded up to 5,164,148 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 <- 0.0195729537366548                          # control proportion
p1 <- 0.0193321616871705                          # 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(1349322)
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 = 5,164,148 (80% power), 6,913,328 (90% power)
 75% of observed effect: n per arm = 9,194,631 (80% power), 12,309,001 (90% power)
 50% of observed effect: n per arm = 20,719,245 (80% power), 27,737,189 (90% power)
power.prop.test: 5164147 
Simulated power at n = 5,164,148 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. Analyses Reported by the Sponsor

The registry's sponsor-reported primary analysis is a Cox regression non-inferiority analysis, with hazard ratio 1.32, 90% confidence interval 0.84 to 2.05, and p = 0.039. It uses time-to-event information and is not the same as an unadjusted comparison of the posted five-year percentages.

The simple re-calculation from the percentages gives a risk difference of -< 0.001, 95% confidence interval -0.012 to 0.011, and p = 0.967. The record flags a discrepancy between the sponsor's result and the simple re-calculation. In that situation, the sponsor's own analysis takes precedence; the recalculation is a separate, unadjusted check and should not be used to overturn the reported analysis.

The two analyses differ in both their statistical quantity and their treatment of follow-up. The risk difference compares percentages at a specified time using posted summaries. The Cox analysis compares hazards over time and is reported as the trial's non-inferiority analysis. The registry does not report the non-inferiority margin or the criterion used to make a formal conclusion, so the reported p-value and interval cannot be independently translated into a declaration that non-inferiority was established.

For the sponsor result, readers should retain the reported model, confidence level, and non-inferiority framing. The re-calculation can help clarify how the arm-level percentages compare, but it answers a narrower question and does not reproduce the sponsor's analysis.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 12 outcome measures and reports nine secondary outcomes. It does not report how the trial handled multiplicity across the primary and secondary outcomes, whether outcomes were ordered in a formal testing hierarchy, or whether p-values were adjusted. Without that information, separate unadjusted secondary p-values should not be treated as if each were an isolated confirmatory test. Multiple testing can increase the chance of a nominally unusual result across a family of analyses.

The primary analysis is identified as non-inferiority, but the non-inferiority margin, the rationale for that margin, and the exact decision rule are not reported in the registry record. Those details are necessary to assess whether the reported hazard-ratio interval meets the trial's non-inferiority criterion. The original sample-size assumptions and design justification are also not reported; the planning illustrations based on observed effects are not a substitute for those original assumptions.

The record describes censoring at last known follow-up and death without in-breast recurrence as a competing event for the primary endpoint. It does not report detailed procedures for other missing outcome data, loss to follow-up by arm, or sensitivity analyses. The registry also does not identify the analysis population used for each result, such as whether analyses followed intention-to-treat principles or a different population definition. These omissions limit independent assessment of the handling of missingness and protocol deviations.

Randomization and parallel allocation are reported, but the record does not provide details of allocation concealment, stratification, adherence, crossovers, or the full statistical analysis plan. No assumption should be made about interim analyses or their boundaries; such details are not reported in the registry record.

These limitations do not establish that the analyses were conducted improperly. They identify information needed to judge the strength and reproducibility of the inferences. The posted results can be described as reported, while conclusions about multiplicity control, missing-data robustness, and the non-inferiority decision framework remain constrained by what the registry records.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: dermatitis radiation (0.3%), breast pain (0.3%), localized edema (0.2%), lung infection (0.2%), fatigue (0.2%).

For the standard-fractionation arm, the registry reports 18 participants with a serious adverse event among 1100 at risk. For the hypofractionated arm, it reports 20 participants with a serious adverse event among 1123 at risk. These are counts of participants affected, not counts of every event, and the record describes the adverse-event outcome as events definitely, probably, or possibly related to protocol treatment.

The record also reports other adverse-event counts of 866 among 1100 at risk in the standard-fractionation arm and 910 among 1123 at risk in the hypofractionated arm. These should be read separately from the serious adverse-event figures. The registry lists dermatitis radiation and breast pain at 0.3% each among the top serious terms; localized edema, lung infection, fatigue, and breast infection are each listed at 0.2%.

These summaries do not show event timing, duration, recurrence, or severity distributions beyond the recorded categories. The reported deaths are 87 and 86, but the registry summary does not establish that these deaths were adverse events related to protocol treatment. The figures should not be interpreted as proof that one treatment strategy is safer.

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

The results describe two randomized radiation strategies and their posted outcomes; they do not establish that the strategies are identical. The five-year in-breast recurrence estimates are close in the posted summaries, and the unadjusted re-calculation produces a risk-difference interval that includes zero. Neither observation is, by itself, a formal demonstration of equivalence or non-inferiority.

The sponsor reports a Cox regression non-inferiority analysis with hazard ratio 1.32, 90% confidence interval 0.84 to 2.05, and p = 0.039. Because the non-inferiority margin and decision criterion are not reported in the registry record, readers cannot independently determine from that summary whether the protocol's criterion was met. The flagged discrepancy also means the sponsor's own analysis takes precedence over the simple recalculation.

The result applies to the treatment strategies as compared in this trial: hypofractionated whole-breast irradiation with concurrent boost versus standard-fractionation whole-breast irradiation with sequential boost. It does not isolate the separate effects of fractionation and boost timing. The listed population is patients with early-stage breast cancer removed by surgery; the registry does not provide enough detail in this summary to extend the conclusions to other populations or treatment settings.

Five-year estimates should not be mistaken for outcomes at the maximum follow-up of 10.1 years. Nor do the posted summaries establish long-term patterns beyond the reported analyses. Secondary outcomes broaden the context but have their own definitions and statistical limitations, including the absence of reported multiplicity handling.

Statistical results do not determine an individual's care. They summarize outcomes in the trial population under the analyses reported in the registry. The evidence supports describing the observed estimates and their uncertainty; stronger claims about equivalence, non-inferiority, or comparative safety require details that are not reported in the registry record.

18. Why This Trial Matters Statistically

This trial presents several statistical issues common in comparative clinical research. The primary outcome is a time-to-event endpoint with a competing event, so the analysis must account for more than a simple comparison of event percentages. The cumulative incidence estimate addresses the event probability in the presence of competing deaths, while the Cox analysis summarizes relative cause-specific hazards. Understanding which quantity answers which question is essential to interpreting the result.

The trial also illustrates why a close pair of point estimates does not automatically establish that two strategies are equivalent. Non-inferiority requires a margin set in advance, along with a compatible analysis and decision rule. The registry reports a non-inferiority analysis but does not report the margin, leaving an important part of the interpretation unavailable to readers.

The contrast combines two treatment features: fractionation and boost timing. This makes the randomized comparison clinically coherent as a strategy-level contrast, but it limits statistical attribution. The results cannot identify the independent contribution of each feature from the posted comparison alone.

Finally, the difference between the sponsor's time-to-event analysis and a simple re-calculation from the five-year summaries shows why analysis methods matter. The re-calculation is not a replacement for the sponsor analysis, particularly when the record flags a discrepancy. Secondary outcomes and safety summaries also require careful treatment because multiple endpoints, different event definitions, and incomplete reporting can affect how much weight a result deserves.

These features make the record useful for learning how endpoint definition, competing risks, non-inferiority, confidence intervals, and analysis transparency shape interpretation. They also show why statistical conclusions should be tied to the exact estimand and analysis reported, rather than inferred from a point estimate alone.

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.

The registry reports no non-inferiority margin or formal decision rule for the primary analysis. As a result, the sponsor's non-inferiority conclusion cannot be independently assessed from the posted summary, despite the reported hazard ratio, confidence interval, and p-value. The record also flags a discrepancy between the sponsor analysis and a simple unadjusted re-calculation; the sponsor's own analysis takes precedence, but the available record does not explain the discrepancy in detail.

The randomized comparison changes both fractionation and boost timing. Any observed contrast therefore pertains to the combined strategies, not the isolated effect of either treatment component. The record identifies no masking, which may be relevant for assessment of outcomes such as cosmetic ratings, but the registry summary does not establish whether or how this affected measurement.

Although maximum follow-up at analysis was 10.1 years, the reported primary estimates are five-year rates. The registry summary does not provide arm-specific follow-up distributions, detailed loss-to-follow-up information, or missing-data sensitivity analyses. It also does not report the analysis population, adherence, crossovers, endpoint adjudication procedures, or diagnostic checks for the reported models.

Nine secondary outcomes are posted out of 12 listed outcome measures. The registry does not report multiplicity procedures or a testing hierarchy, which limits the strength of interpretation for secondary p-values. The original sample-size assumptions and justification are not reported; retrospective planning illustrations based on observed effects do not recover that information.

These are limitations of the information available in the registry record, not proof that the trial lacked procedures or analyses. They constrain what can be independently concluded from the posted summary.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Higher Per Daily Treatment-Dose Radiation Therapy or Standard Per Daily Treatment Radiation Therapy in Treating Patients With Early-Stage Breast Cancer That Was Removed by Surgery — NCT01349322.
• Registry record last updated 2026-03-05; status last verified 2025-09.
• Results first posted 2023-04-06.
• 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

NCT01349322 is a randomized phase III parallel-group trial, with no masking, comparing hypofractionated whole-breast irradiation plus concurrent boost with standard-fractionation whole-breast irradiation plus sequential boost after surgery for early-stage breast cancer. The primary outcome is five-year in-breast recurrence, estimated using the cumulative incidence method with death without recurrence treated as a competing event.

The registry reports arm-level five-year recurrence estimates of 2.0% and 1.9%. The sponsor's primary analysis is a Cox regression non-inferiority analysis, reporting hazard ratio 1.32, 90% confidence interval 0.84 to 2.05, and p = 0.039. The non-inferiority margin is not reported. A discrepancy is flagged, so the sponsor's analysis takes precedence over the unadjusted re-calculation.

The record lists 12 outcome measures and posts nine secondary outcomes. Important details about multiplicity, missing-data procedures, analysis populations, and original sample-size justification are not reported in the registry record.