Early Surgery or Standard Palliative Therapy in Treating Patients With Stage IV Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Early Surgery or Standard Palliative Therapy in Treating Patients With Stage IV Breast Cancer (NCT01242800), a randomized na study. The primary outcome is 3-year Overall Survival Rate.

2. Clinical Question

The trial asks whether early local treatment of the intact breast primary tumor is associated with a different overall-survival pattern than standard palliative therapy among patients with stage IV breast cancer. The registry describes a randomized comparison and identifies three-year overall survival as the primary outcome.

The rationale in the registry is that a primary tumor might contribute to the reseeding of distant sites, so early local treatment was studied as a way to remove that possible source. That rationale is not itself evidence that the strategy changes survival. The posted outcome estimates and their uncertainty are the relevant evidence for describing the trial’s results.

The title and summary call the study a randomized phase III trial, while the registry’s phase classification is listed as NA. The registry record does not report additional detail about the hypothesis that determined the primary comparison or the expected size of an effect.

3. Trial Design

The registry describes a randomized, open-label, parallel-group study comparing early local therapy with standard palliative therapy in stage IV breast cancer. The study status is completed, and enrollment is listed as 390. The primary outcome population is narrower: the registry identifies all randomized patients at step 2 and reports 131 participants in Arm I and 125 in Arm II for the three-year overall-survival outcome. The registry record does not explain the relation between total enrollment and the step 2 population.

What the arms involved

Arm I is titled Continued Systemic Therapy. Its description says standard palliative treatment could be given if needed for symptoms such as tumor ulceration, pain, or bulky adenopathy causing arm symptoms. Possible treatment included radiotherapy alone, surgery alone, or both. Arm II is titled Early Local Therapy. Its description specifies breast-conserving therapy or total mastectomy according to patient and treating physician preference. Surgery was to take place no later than 10 weeks after completion of 32 weeks of systemic therapy.

The registry’s Arm II description ends mid-sentence after referring to free surgical margins and re-excision. Further details of that statement are not reported in the registry record. The registry lists both palliative and conventional surgery, as well as palliative and other radiation therapy, among the interventions.

Outcome follow-up

Overall survival was assessed at baseline and then every 3 months within 2 years and every 6 months between 2 and 5 years, up to 5 years. The registry defines the outcome as time from randomization to death from any cause, with censoring at last contact for incomplete follow-up or when vital status was unavailable. It reports the three-year rate as estimated with the Kaplan-Meier method.

The registry does not report the method used to generate the random sequence, concealment procedures, or additional details about adherence and treatment crossover. Masking is listed as none. The phase classification field is NA, although the study title and summary describe a randomized phase III trial.

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: All randomized patients at step 2

5. Baseline Characteristics

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

Population: All randomized patients at step 2

6. Primary Endpoint

The registry lists the primary outcome as 3-year Overall Survival Rate, measured over Assessed at baseline, then every 3 months within 2 years and every 6 months between 2-5 years, up to 5 years.

The primary endpoint is the three-year overall-survival rate, expressed as a percentage of participants. Overall survival measures time from randomization until death from any cause. Participants whose follow-up was incomplete, or whose vital status was not recorded, were censored at their last contact according to the registry description.

Time-to-event outcomes such as overall survival use information about when an event occurs, not just whether it occurred by a chosen date. The registry says the three-year rate was estimated with the Kaplan-Meier method. This approach can use participants’ observed follow-up up to the point they are censored, rather than treating everyone without a recorded death at the analysis time as having identical follow-up.

Overall survival is used because it captures death from any cause and is directly interpretable as survival over time. The three-year rate is a snapshot at a specified follow-up point, while the underlying survival analysis concerns event timing over follow-up. A rate at one time point therefore does not, by itself, describe the full survival experience or establish how treatment groups compare across the entire follow-up period.

The registry also reports a log-rank analysis, a method that compares time-to-event patterns across groups. Its result is distinct from an unadjusted comparison recalculated from the posted three-year rates. The two analyses use different representations of the survival data and should not be treated as interchangeable.

7. Results Posted in the Registry

• Arm II (Early Local Therapy): 68.8% (86/125) versus 67.9% (89/131) on control; risk difference 0.9 percentage points (95% CI -10.5 to 12.3), risk ratio 1.01 (0.86–1.20); unadjusted two-proportion z-test p = 0.882.

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.

3-year Cumulative Incidence of Locoregional Recurrence/Progression

• 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:
  • Arm II (Early Local Therapy): 40.0% (50/125) versus 16.0% (21/131) on control; risk difference 24.0 percentage points (95% CI 13.3 to 34.6), risk ratio 2.50 (1.60–3.90); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Arm II (Early Local Therapy) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Health-related Quality of Life (HRQL)

• 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 II (Early Local Therapy): mean 68.00 versus 74.20 on control; difference -6.20 (95% CI -10.53 to -1.87), standardized effect d = -0.49; z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Arm II (Early Local Therapy) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes concern local recurrence or progression and health-related quality of life, rather than survival. In broad terms, the posted patterns are not uniform across outcome domains: the primary survival estimates are close, while the secondary results suggest different group patterns for local disease events and quality-of-life scores. These outcomes offer additional context about what happened in the trial, but they do not directly answer the primary overall-survival question.

Locoregional recurrence or progression is a disease-control outcome, while health-related quality of life is a patient-reported or score-based outcome assessed at 18 months after randomization. Each measures a different aspect of experience. A result in one domain cannot be assumed to cause or explain a result in another, and the registry does not report an analysis connecting the secondary outcomes to the primary survival result.

The secondary comparisons are unadjusted recalculations, and no sponsor-reported analyses are listed for them. The registry record does not say whether these outcomes were part of a prespecified testing sequence or whether multiplicity was controlled. When several outcomes are examined, the chance of observing a nominally notable result can increase; in general, this is why unadjusted secondary p-values carry less evidential weight than a prespecified primary analysis. The secondary results remain informative descriptions, but their inferential strength should not be overstated.

The registry lists confidence intervals for the locoregional outcome and mean and standard-deviation summaries for quality of life. These provide outcome-specific information about estimates and variability. They do not resolve unreported questions about missing observations, analysis populations, or adjustment for multiple testing.

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

• 3-year Cumulative Incidence of Locoregional Recurrence/Progression
• Health-related Quality of Life (HRQL)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is a time-to-event outcome. For each participant, the event is death from any cause, and time begins at randomization. The registry states that the three-year overall-survival rate was estimated with the Kaplan-Meier method. This method estimates the probability of remaining event-free over time while accounting for participants whose event status is not observed through the full follow-up period.

Censoring and Kaplan-Meier estimation

Censoring occurs when a participant’s follow-up ends before a death is recorded or before the analysis period is complete. The registry says that incomplete follow-up or missing vital-status information leads to censoring at the date of last contact. A censored participant contributes information up to that contact, but their later survival status is not known from the record. Kaplan-Meier estimation relies on the observed follow-up and censoring pattern; it does not make an unknown later status into a known survival outcome.

The three-year rate is a point on an estimated survival curve. It summarizes survival at that time, but it does not show the full shape of the curve. Two groups can have similar estimated rates at one time while their event timing differs at other times. Conversely, a difference at one time point does not alone describe the entire time-to-event pattern.

Log-rank comparison

The registry reports a log-rank test for the two groups, with p = 0.32. In general, a log-rank test compares the timing of events over follow-up, taking account of the risk sets at event times. Its p-value evaluates how compatible the observed separation in event experience is with a null hypothesis of no group difference, under the test’s assumptions. It is not an effect-size estimate and does not state the probability that a treatment effect exists.

The registry does not report a hazard ratio, a confidence interval for a hazard ratio, or details of any stratification or covariate adjustment. Those quantities should not be inferred from the log-rank p-value. The outcome description identifies Kaplan-Meier estimation, but the registry record does not give more detail about the statistical plan for the primary analysis.

Unadjusted recalculations

The recalculated comparisons are simple, unadjusted comparisons based on the posted summary statistics. For the primary result, the recalculation compares the posted three-year rates as a binary-type outcome and reports a risk difference, confidence interval, and p-value. It does not reproduce the log-rank analysis because it does not use the individual event times or the full survival curves. It is therefore a supplementary summary, not a replacement for the registry’s reported time-to-event result.

For the secondary locoregional outcome, the registry posts percentages and a recalculated unadjusted risk comparison. For health-related quality of life, it posts group means and standard deviations, with an unadjusted mean difference. In general, a risk difference describes the contrast in event probabilities between groups, while a mean difference describes the contrast in average scores. These summaries depend on the particular outcome definition and analysis population; they do not automatically adjust for baseline differences or other covariates.

Confidence intervals and p-values

A confidence interval gives a range of effect values compatible with the observed data under the method used and its assumptions. A wider interval indicates less precision. A p-value is a measure of how unusual the observed data, or more extreme data, would be under a specified null hypothesis and analysis. Neither measure alone answers whether an effect is clinically important. The clinical importance of a difference requires context that is not reported in the registry record.

The registry reports 95% confidence intervals for the primary group-specific estimates. The recalculated contrasts also include confidence intervals. These intervals are useful for seeing the plausible range of values under each analysis, but intervals from separate groups are not a substitute for an interval on the between-group contrast. The recalculated contrast interval is the relevant summary for that unadjusted comparison.

Uncertainty and dispersion

In general, outcome estimates have sampling uncertainty because the observed participants are one sample from a broader population of interest. Greater variability, fewer observations, or fewer events can reduce precision. Time-to-event precision also depends on the event and censoring information accumulated over follow-up. The registry does not report the full event-time dataset or detailed precision calculations, so the posted estimates and intervals are the available basis for interpretation.

For continuous outcomes, standard deviation describes variation among individual scores, whereas a confidence interval around a mean or mean difference describes uncertainty about the estimated average. These answer different questions. The health-related quality-of-life standard deviations therefore should not be read as confidence limits.

11. Confidence Intervals and Precision

The primary group estimates have 95% confidence intervals of 58.8% to 75.5% for Arm I and 59.0% to 76.1% for Arm II. These ranges are wide enough to show meaningful uncertainty around each three-year rate. Their overlap is substantial, and the point estimates are close, but overlap between separate group intervals is not itself a formal test of the treatment contrast.

Precision for a comparison is best judged using the interval for the contrast. The unadjusted recalculation has a risk-difference interval that extends in both directions around no difference. This means the summary-based estimate does not precisely determine which group has the higher three-year rate. It also does not establish that the true difference is exactly zero. The sponsor-reported log-rank p-value is 0.32, but the registry does not report a confidence interval for the sponsor’s time-to-event contrast.

Confidence intervals are ranges generated by a statistical method. In repeated use under its assumptions, a 95% confidence-interval procedure would capture the target parameter in 95% of comparable repetitions. It is not correct to interpret a particular interval as assigning a 95% probability to the parameter after the data have been observed.

The secondary outcomes have their own uncertainty and should not be judged by the primary endpoint’s precision. Their sample sizes differ from the primary outcome population, and the registry does not explain the reasons for those differences. The uncertainty in any result depends on the outcome, the analysis population, and the available observations, not simply on total study enrollment.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are illustrations based on the observed effect, not the trial’s original design. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a specified fraction of the observed effect as the effect to detect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

For the binary-type outcomes, the figures are participants per arm. For a time-to-event planning calculation, the figures would be total events, but the posted primary planning rows are based on the recalculated three-year rate comparison, so the displayed quantities are participants per arm. They are not totals across both arms.

The 80% power column means the planned chance of detecting an effect of the specified size under the stated assumptions would be 80%, if that effect were real and the assumptions held. The 90% power column expresses the corresponding planning target at 90%. Higher power generally requires more participants for the same effect size and assumptions.

Each row considers a different fraction of the observed effect. A smaller effect is harder to detect, so the planning figures increase as the target effect becomes smaller. For example, planning for 50% of the observed effect requires more participants per arm than planning for the full observed effect. These are prospective planning illustrations, not observed power and not evidence that the trial had a particular probability of detecting its actual effect.

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 = 0.679; treatment proportion p₁ = 0.688; average p̄ = 0.684.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6577 = 1.2890.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6576 = 0.5535.
4. n = (1.2890 + 0.5535)² / (0.0086)² = 45,784.6, rounded up to 45,785 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 <- 0.679389312977099                          # control proportion
p1 <- 0.688                          # 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(1242800)
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 = 45,785 (80% power), 61,293 (90% power)
 75% of observed effect: n per arm = 81,545 (80% power), 109,165 (90% power)
 50% of observed effect: n per arm = 183,808 (80% power), 246,067 (90% power)
power.prop.test: 45784.6 
Simulated power at n = 45,785 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 reported primary analysis is a log-rank test, with p = 0.32. That is the sponsor-reported time-to-event analysis and takes precedence over the simple recalculation for interpreting the primary comparison. The registry does not report a corresponding hazard ratio or confidence interval, so the magnitude and precision of the sponsor’s time-to-event contrast cannot be described from those fields.

The recalculated p-value of 0.882 comes from an unadjusted comparison of the posted three-year rates. It is not a correction or confirmation of the log-rank test. The recalculation uses a summary contrast at one time point, whereas the log-rank analysis uses event timing over follow-up. Differences between these p-values can arise because the analyses use different information and test different summaries; the registry record does not provide enough detail to attribute the difference to a particular cause.

The recalculation is useful as a transparent secondary description of the posted rates, but it should not replace the sponsor’s stated primary method. The registry does not indicate a discrepancy between the recalculation and sponsor result. Both results should be identified by their analysis methods rather than treated as competing estimates of the same statistic.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies overall survival as the primary outcome and lists two secondary outcomes: locoregional recurrence or progression and health-related quality of life. It does not report a multiplicity strategy, such as an adjustment procedure, a testing hierarchy, or a rule for interpreting the secondary outcomes. Without that information, the secondary p-values should be regarded as unadjusted and exploratory in their statistical interpretation.

Multiplicity matters because testing multiple outcomes can raise the chance of at least one apparently unusual result under a setting in which none of the effects is real. This general statistical issue does not mean that a secondary finding is false. It means that the strength of evidence is harder to assess when the number and ordering of planned tests are not known.

The primary outcome description says that cases with incomplete follow-up or without a record of vital status were censored at last contact. The registry does not report the number of censored participants, the amount of missing vital-status information, or sensitivity analyses for missing follow-up. It also does not provide a detailed missing-data approach for the secondary outcomes, including the quality-of-life assessment at 18 months.

The primary outcome population is described as all randomized patients at step 2. The registry does not explain how this population relates to the total enrollment of 390, nor does it detail exclusions or analysis-set definitions. For quality of life, the posted group sample sizes are 65 and 66; the reasons that these numbers are smaller than the primary outcome group sizes are not reported in the registry record. No assumptions about missingness or participant availability should be inferred from those counts alone.

The registry does not report subgroup analyses, interim analyses, or further details of the statistical analysis plan. Their presence or absence cannot be established from the posted record. Such unreported details limit assessment of how analyses were selected and how robust the findings are to alternative analytic choices.

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

The posted primary results describe three-year overall-survival estimates of 67.9% in Arm I and 68.4% in Arm II, with overlapping 95% confidence intervals. The registry’s log-rank analysis reports p = 0.32. Together, these describe the observed survival data and the uncertainty available in the registry; they do not demonstrate that the groups are equivalent, and they do not rule out every potentially important difference.

A failure to identify a statistically compelling difference is not proof of no effect. Equivalence or non-inferiority conclusions require an appropriate design and prespecified margins, which are not reported in the registry record. Similarly, a p-value does not state the probability that a treatment works or does not work, and the survival estimates alone do not establish a causal mechanism.

The secondary findings address different outcomes. A local recurrence or progression measure is not the same as overall survival, and a quality-of-life score is not a survival measure. These results should be considered on their own terms and with the limitations of unadjusted secondary analyses and unreported missing-data details.

The findings apply to the trial’s enrolled population and the treatment strategies as described in the registry. The available record does not establish how the results would apply to other populations, settings, or treatment approaches. It also does not provide enough information to judge the clinical importance of a particular numerical difference using a threshold for meaningful change.

These statistical results are not medical advice. They describe estimates, comparisons, and uncertainty reported for this study, rather than directing an individual treatment decision.

17. Why This Trial Matters Statistically

This trial is statistically instructive because it compares a time-to-event primary outcome with simple summary-based recalculations. The registry’s primary result is a log-rank analysis, which uses event timing over follow-up. A recalculated comparison of three-year rates is easier to interpret as a single-time-point contrast, but it is not the same statistical test. Understanding that distinction prevents a summary calculation from displacing the reported primary analysis.

The example also shows why effect estimates and uncertainty matter alongside p-values. The posted survival rates are close, and their confidence intervals are broad. A p-value alone cannot convey the range of plausible differences, while group-specific confidence intervals are not a substitute for an interval on the between-group contrast. The result should be read as an estimate with uncertainty, rather than as a definitive statement of equality or difference.

Another important issue is the distinction between outcomes. Overall survival, local recurrence or progression, and quality of life capture separate aspects of a trial. A pattern in a secondary outcome does not automatically overturn, explain, or predict the primary outcome. Unadjusted secondary tests also require cautious interpretation when the testing plan is not reported.

Finally, enrollment and endpoint-specific analysis populations are not interchangeable. The total enrollment is 390, while the registry gives smaller outcome-specific counts and identifies the primary population as randomized patients at step 2. Because the registry does not explain this relationship, careful reading means reporting the populations as stated without inferring why they differ.

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.

The registry record leaves several design and analysis details unspecified. It does not provide the original sample-size justification, the planned effect size, or details of the statistical analysis plan. The planning illustrations based on observed effects cannot fill that gap. The registry also does not report random-sequence generation or allocation concealment procedures.

The primary outcome population is described as all randomized patients at step 2, but the record does not explain how this relates to total enrollment. The numbers contributing to the secondary outcomes are also different, and the reasons are not reported. In particular, the quality-of-life outcome has fewer participants than the primary outcome groups; the record does not state whether this reflects missing questionnaires, eligibility, follow-up availability, or another reason.

The registry does not report the number of censored participants, the amount of missing follow-up, or sensitivity analyses for missing data. It provides the primary log-rank p-value but no hazard ratio or confidence interval for that analysis. This limits assessment of the size and precision of the sponsor-reported time-to-event contrast.

The Arm II description is truncated after the reference to free surgical margins and re-excision, so its full protocol details are not available in the registry record. The record also does not provide details about treatment adherence, crossover, or the timing and extent of treatments received beyond the summary description. Masking is listed as none, which is relevant context for outcomes that may be influenced by awareness of treatment assignment.

Finally, the registry does not report a multiplicity plan or additional analyses of the secondary outcomes. These omissions constrain interpretation but do not, by themselves, establish that the analyses were improperly conducted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Early Surgery or Standard Palliative Therapy in Treating Patients With Stage IV Breast Cancer — NCT01242800.
• Registry record last updated 2023-06-29; status last verified 2023-06.
• Results first posted 2023-02-02.
• 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 describes a completed randomized, open-label, parallel-group comparison of early local therapy and standard palliative therapy in stage IV breast cancer. Enrollment is listed as 390. The primary endpoint is three-year overall survival among all randomized patients at step 2, estimated using Kaplan-Meier methods.

The posted three-year survival estimates are 67.9% for Arm I and 68.4% for Arm II, with 95% confidence intervals of 58.8% to 75.5% and 59.0% to 76.1%, respectively. The sponsor-reported log-rank p-value is 0.32. The registry also lists locoregional recurrence or progression and health-related quality of life as secondary outcomes.

Several details needed for fuller assessment, including original sample-size assumptions, multiplicity procedures, and secondary-outcome missing-data methods, are not reported in the registry record.