Platinum in Treating Patients With Residual Triple-Negative Breast Cancer Following Neoadjuvant Chemotherapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Platinum in Treating Patients With Residual Triple-Negative Breast Cancer Following Neoadjuvant Chemotherapy (NCT02445391), a randomized phase 3 study. The primary outcome is 3-year Invasive Disease-Free Survival (IDFS) Rate in Basal-Subtype Patients.

2. Clinical Question

The clinical context is residual disease after chemotherapy given before surgery. The trial asks whether postoperative platinum-based chemotherapy, using cisplatin or carboplatin, compares with capecitabine in this population. The primary outcome is a time-to-event measure: it captures the time from randomization to the earliest qualifying event rather than only whether a participant had an event at a single visit.

The registry record identifies a basal-subtype population for the primary analysis, rather than all participants enrolled in the trial. The reported primary rates and sponsor analysis concern the two concurrently randomized treatment arms after 6/22/2016. Arm A, observation, is described separately and was closed to accrual 05/16/2016; it is not one of the two arms in the posted primary comparison.

3. Trial Design

This was a randomized, phase III, parallel-group trial with no masking. The registry record lists enrollment of 415 and identifies ECOG-ACRIN Cancer Research Group as the sponsor. The recorded start date is 2015-10-20, primary completion date is 2021-04-07, and status is active, not recruiting.

The registry describes three arms. Arm A involved observation and was closed to accrual 05/16/2016. Arm B involved cisplatin or carboplatin, and Arm C involved capecitabine. The primary analysis was restricted to basal-subtype TNBC patients concurrently randomized to Arms B and C after 6/22/2016. Consequently, the primary comparison is not a comparison of every arm listed in the trial record, and the enrollment figure should not be read as the size of the primary analysis population.

For Arm B, the listed regimen was cisplatin or carboplatin intravenously on day 1, repeated every 3 weeks for 4 courses unless disease progression or unacceptable toxicity occurred. For Arm C, the listed regimen was capecitabine orally twice daily on days 1–14, repeated every 3 weeks for up to 6 courses unless disease progression or unacceptable toxicity occurred. The record does not specify how the choice between cisplatin and carboplatin was made.

The posted primary outcome is the 3-year invasive disease-free survival rate in basal-subtype patients. Secondary outcomes include recurrence-free survival and overall survival rates at 3 years, the proportion with basal subtype, and health-related quality of life at the 6-month and 15-month assessments. The registry record posts results for five secondary outcomes. The registry record does not report the trial’s original sample-size justification, detailed randomization procedures, or the full statistical 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.

Before assignment: Before randomization patients were tested about their intrinsic subtype using PAM50 assay at step 0. Before amendment #3, only basal subtype was eligible and was randomized. After amendment #3, all patients were eligible regardless of intrinsic subtype, and intrinsic subtype was added as a stratification factor. After amendment #7 (activated in November 2020), intrinsic subtype was no longer a stratification factor, patients were randomized as long as tumor specimen was submitted for PAM50 test.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The primary analysis population was all basal-subtype TNBC patients who were concurrently randomized to arms B and C after 6/22/2016 (intent-to-treat 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: All patients who were concurrently randomized to arms B and C after 6/22/2016 and had basal-subtype disease, this was the primary analysis population for IDFS and other secondary efficacy endpoints (OS and RFS). Only patients included in the primary analysis are included in the analysis of baseline characteristics.

6. Primary Endpoint

The registry lists the primary outcome as 3-year Invasive Disease-Free Survival (IDFS) Rate in Basal-Subtype Patients, measured over No mandatory timeline, assessed at any time as a standard of care procedure or at the investigator's discretion; data reported every 3 months within 2 years from randomization, every 6 months if 2-3 years..

Invasive disease-free survival (IDFS) was defined as the time from randomization to the earliest of documented disease recurrence, invasive cancer in the opposite breast, another invasive second cancer, or death. This composite endpoint counts several clinically important events as failures, so the measure captures more than recurrence of the original breast cancer alone.

The registry record says cases with incomplete follow-up or without adequate disease evaluations were censored at the date last documented to be free of IDFS events. The 3-year IDFS rate was estimated using the Kaplan-Meier method. In general, Kaplan-Meier estimation uses the observed event times while allowing follow-up to end at different times; censoring records the last known event-free time without treating that time as an event.

A 3-year rate gives a fixed-time summary of the estimated event-free experience, while the underlying endpoint uses time to the first qualifying event. This can be useful when participants have differing follow-up durations. However, the rate alone does not describe when events occurred, which component events contributed, or how the estimate changes over time. Those details are not reported in the registry record.

The primary analysis concerns the specified basal-subtype population concurrently randomized to the treatment arms after 6/22/2016. The posted primary estimates are 42.0% for cisplatin or carboplatin and 49.4% for capecitabine, each with a 95% confidence interval. These are estimates, not exact underlying population rates.

7. Results Posted in the Registry

• Arm C (Capecitabine) (Open to Accrual 6/22/2016): 49.4% (79/160) versus 41.9% (62/148) on control; risk difference 7.5 percentage points (95% CI -3.6 to 18.6), risk ratio 1.18 (0.92–1.51); unadjusted two-proportion z-test p = 0.188.

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 Recurrence-Free Survival (RFS) Rate in Basal-Subtype Patients

• 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 C (Capecitabine) (Open to Accrual 6/22/2016): 49.4% (79/160) versus 45.9% (68/148) on control; risk difference 3.4 percentage points (95% CI -7.7 to 14.6), risk ratio 1.07 (0.85–1.36); unadjusted two-proportion z-test p = 0.547.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm C (Capecitabine) (Open to Accrual 6/22/2016) and the control. The interval gives the range of effects that remain compatible with the data.

3-year Overall Survival (OS) Rate in Basal-Subtype Patients

• 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 C (Capecitabine) (Open to Accrual 6/22/2016): 66.2% (106/160) versus 58.1% (86/148) on control; risk difference 8.1 percentage points (95% CI -2.7 to 19.0), risk ratio 1.14 (0.96–1.36); unadjusted two-proportion z-test p = 0.141.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm C (Capecitabine) (Open to Accrual 6/22/2016) and the control. The interval gives the range of effects that remain compatible with the data.

Health-related Quality of Life (HRQL) at 6-month Assessment

• 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 C (Capecitabine) (Open to Accrual 6/22/2016): mean 14.60 versus 14.70 on control; difference -0.10 (95% CI -0.66 to 0.46), standardized effect d = -0.06; z-test p = 0.726.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Arm C (Capecitabine) (Open to Accrual 6/22/2016) and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover recurrence-free survival and overall survival at 3 years, along with health-related quality of life at the 6-month and 15-month assessments. The registry record reports results for five secondary outcomes, but does not post a sponsor analysis for those outcomes. Together, they offer additional views of disease events, survival, and reported quality of life rather than a single interchangeable measure.

At a broad level, the survival-rate estimates do not supply a decisive contrast that resolves the uncertainty in the primary IDFS comparison. The quality-of-life result is a score on a scale and addresses a different kind of outcome; it should not be read as a survival estimate or as a direct explanation of the primary result. These measures may complement the primary endpoint, but they cannot replace it.

The secondary results carry less inferential weight when considered individually because they are additional comparisons beyond the primary question. In general, testing many outcomes can increase the chance of observing an apparently notable result by chance. The registry record does not report a multiplicity adjustment, a hierarchy for interpreting these secondary outcomes, or a complete statistical analysis plan. Their unadjusted comparisons should therefore be treated as exploratory or descriptive rather than as independent confirmation of a treatment difference.

Differences in endpoint definition, follow-up, and measurement also matter. Recurrence-free survival, overall survival, and quality-of-life scores do not answer the same question as IDFS. The posted secondary evidence can help characterize the trial, but the registry record does not give enough methodological detail to establish how these outcomes were prioritized or jointly interpreted.

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

• 3-year Recurrence-Free Survival (RFS) Rate in Basal-Subtype Patients
• 3-year Overall Survival (OS) Rate in Basal-Subtype Patients
• Proportion of Basal Subtype
• Health-related Quality of Life (HRQL) at 6-month Assessment
• Health-related Quality of Life (HRQL) at 15-month Assessment

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary endpoint is a time-to-event outcome, but the headline result is expressed as an estimated 3-year rate. These are related but distinct ways of presenting the evidence. Time-to-event methods use both whether an event occurred and when it occurred. A fixed-time rate summarizes the estimated event-free proportion at a selected time point. In general, this approach can use participants with different lengths of follow-up, provided the method’s assumptions are suitable.

What does Kaplan-Meier estimation do?

The registry record states that the 3-year IDFS rate was estimated using the Kaplan-Meier method. In general, this method updates the estimated probability of remaining event-free as events occur during follow-up. Participants whose follow-up ends before an event are censored at their last documented event-free time, rather than counted as having experienced an event at that time. For the primary outcome, the record specifically says that incomplete follow-up or inadequate disease evaluations were censored at the last date documented as free of an IDFS event.

Censoring is not the same as proof that no later event occurred. It indicates that the event-free status was documented through a particular time, after which the registry’s described analysis no longer has adequate event information for that participant. General survival analysis relies on assumptions about how censoring relates to future event risk. The registry record does not report diagnostic checks or further details on those assumptions.

How should the posted rate comparison be distinguished from the sponsor analysis?

The arm-specific rates have 95% confidence intervals. Separately, the simple recalculation reports a risk difference of 0.075, a 95% confidence interval from -0.036 to 0.186, and an unadjusted p-value of 0.188. This is an unadjusted comparison of the posted summaries. It does not reproduce a full time-to-event model, account for any unreported covariates, or substitute for the sponsor’s analysis.

The sponsor’s reported result is a hazard ratio of 1.06 with a 95% confidence interval from 0.62 to 1.81, described as a non-inferiority analysis. In general, a hazard ratio compares event rates over follow-up as represented by a time-to-event model. It is not a percentage-point difference in 3-year rates. The registry record does not report the model method, a p-value, or the non-inferiority margin. Those omissions limit interpretation of the sponsor result as a formal non-inferiority test.

What do confidence intervals and p-values contribute?

In general, a confidence interval shows a range of values compatible with the observed data under the analysis method and its assumptions. It communicates precision as well as direction: a wider interval leaves more uncertainty about the underlying effect. A p-value summarizes how unusual results at least as incompatible with a specified null hypothesis would be if that hypothesis and the statistical model were true. It is not the probability that the null hypothesis is true, and it does not quantify the chance that a treatment is beneficial.

The unadjusted risk-difference interval includes zero, and the unadjusted p-value is 0.188. Those features mean that the recalculation does not provide a clear statistical distinction under a conventional null comparison. They do not prove equality, and they do not answer the separate question of whether a prespecified non-inferiority margin was met.

Why does over-dispersion matter in some analyses?

General statistical models sometimes assume that observed variation follows a specified distribution. Over-dispersion occurs when the data vary more than that model allows. If it is ignored, standard errors can be too small and confidence intervals too narrow. The registry record does not describe an over-dispersion assessment for this trial’s primary result, and the posted primary endpoint is a time-to-event rate rather than a simple count model. It would therefore be inappropriate to assume that an over-dispersion adjustment was used or needed.

The record’s endpoint definition also matters. IDFS includes recurrence, invasive contralateral breast cancer, another invasive second cancer, or death. The resulting composite combines different event types into one time-to-first-event outcome. The record does not provide component-specific counts or analyses, so the relative contribution of each type cannot be assessed from the posted primary summary.

11. Confidence Intervals and Precision

The primary arm-specific estimates have substantial uncertainty. For cisplatin or carboplatin, the posted 3-year IDFS rate is 42.0%, with a 95% confidence interval from 30.5 to 53.1. For capecitabine, it is 49.4%, with a 95% confidence interval from 39.0 to 59.0. Each interval covers a range of plausible values under the method and its assumptions; neither endpoint of an interval is a guaranteed limit on the true rate.

The recalculated unadjusted risk difference is 0.075, with a 95% confidence interval from -0.036 to 0.186. Because the interval includes zero and spans values on both sides, the direction and size of the difference are not precisely determined by this recalculation. The unadjusted p-value of 0.188 is consistent with the lack of a clear separation under a simple null comparison, but it does not prove the arms are equivalent.

Confidence intervals are important because point estimates alone can look more definitive than the data warrant. In general, an interval’s width reflects sampling uncertainty under the chosen statistical method; it does not account automatically for every source of bias, measurement error, missing information, or model uncertainty. The registry record does not report enough detail to evaluate all such sources.

The sponsor’s hazard-ratio interval, 0.62 to 1.81, is also broad. It is a different estimand from the unadjusted risk difference, so the two intervals should not be compared as though they measured the same effect. The registry record does not report the margin needed to assess the non-inferiority claim. Overall, the posted summaries leave meaningful uncertainty about comparative outcomes.

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 assumptions. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. For time-to-event outcomes, the figures are the total number of events; for all other outcomes, they are participants per arm. The original design assumptions are not reported in the registry record.

The 80% power column gives the planning number needed per arm for a design with an 80% chance of detecting the specified effect under the stated assumptions, if that effect were the true effect and the model assumptions held. The 90% power column uses a higher target chance of detecting that same specified effect. These are design targets, not guarantees about the result of a future study.

For the primary outcome, planning for 100% of the observed effect gives 695 participants per arm for 80% power and 929 participants per arm for 90% power. Planning for 75% of the observed effect gives 1,231 participants per arm for 80% power and 1,648 participants per arm for 90% power. Planning for 50% of the observed effect gives 2,759 participants per arm for 80% power and 3,693 participants per arm for 90% power. Smaller effects need more participants to detect under these assumptions.

These are not observed power calculations and should not be read as a judgment that the completed trial was adequately or inadequately powered. They are planning illustrations derived from the observed effect, which is itself uncertain. Sample-size planning for a new study would ordinarily require a scientifically chosen target effect and design assumptions, not simply adoption of an observed estimate.

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 = 0.419; treatment proportion p₁ = 0.494; average p̄ = 0.456.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7044 = 1.3806.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7024 = 0.5912.
4. n = (1.3806 + 0.5912)² / (0.0748)² = 694.3, rounded up to 695 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 <- 0.418918918918919                          # control proportion
p1 <- 0.49375                          # 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(2445391)
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 = 695 (80% power), 929 (90% power)
 75% of observed effect: n per arm = 1,231 (80% power), 1,648 (90% power)
 50% of observed effect: n per arm = 2,759 (80% power), 3,693 (90% power)
power.prop.test: 694.3 
Simulated power at n = 695 per arm: 0.804 (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 record reports a sponsor analysis with a hazard ratio of 1.06 and a 95% confidence interval from 0.62 to 1.81. It is labelled as a non-inferiority analysis. The record does not report the model method, p-value, or non-inferiority margin, so the formal criterion and the sponsor’s decision cannot be independently assessed from the posted information.

The recalculated comparison is different: it is an unadjusted risk difference based on the posted arm summaries, estimated as 0.075 with a 95% confidence interval from -0.036 to 0.186 and an unadjusted p-value of 0.188. It is not a reconstruction of the sponsor’s time-to-event analysis. A hazard ratio and a risk difference at 3 years describe different contrasts and use different statistical summaries.

The registry record does not flag a discrepancy between its reported analysis and the recalculation. Even so, the sponsor’s own analysis takes precedence over a simple recalculation when describing the trial’s prespecified or official analysis. The recalculation is useful as a transparent, unadjusted summary, but it cannot establish whether a non-inferiority margin was satisfied. Without that margin and the analysis details, no stronger conclusion about non-inferiority can be drawn from the registry entry alone.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is described as basal-subtype TNBC patients concurrently randomized to Arms B and C after 6/22/2016, with the record identifying it as an intent-to-treat population. That description defines the population for the primary comparison, but the registry record does not provide the full analysis plan or further details about how participants were classified for this population.

The primary endpoint includes censoring for incomplete follow-up or inadequate disease evaluations. The record says those cases were censored at the last date documented to be free of IDFS events. It does not report the amount or pattern of missing follow-up, the number censored, or sensitivity analyses examining how alternative assumptions about missing information might affect the estimate. Censoring should not be interpreted as evidence that an event did not occur after the last documented event-free time.

The registry record lists multiple secondary outcomes, including survival, recurrence, and quality of life. It does not report a multiplicity adjustment or a testing hierarchy that would control the interpretation of multiple outcome comparisons. In general, examining several outcomes can increase the chance that at least one result appears statistically notable even when there is no underlying effect for that outcome. This is why unadjusted secondary comparisons generally carry less weight than a clearly specified primary analysis.

The record also does not report interim analyses, the trial’s original sample-size justification, detailed randomization procedures, or the full statistical analysis plan. The sponsor’s non-inferiority result is reported without the margin or model method. These omissions limit evaluation of whether all analyses followed prespecified procedures and how missing data, multiple outcomes, and the non-inferiority question were handled.

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: white blood cell decreased (9.7%), anemia (7.5%), platelet count decreased (7.5%), diarrhea (5.5%), palmar-plantar erythrodysesthesia syndrome (5.0%).

The adverse-event figures distinguish serious events from other events and identify the number at risk and the number affected in each treatment group. For Arm B, 186 were at risk for serious adverse events and 50 were affected; the same group size is listed for other adverse events, with 141 affected. For Arm C, 201 were at risk for serious adverse events and 32 were affected; 201 were listed at risk for other adverse events, with 165 affected. The observation group lists zero at risk and zero affected for these event categories, with 2 deaths reported.

The most common serious-event terms listed in the record include White blood cell decreased at 9.7%, Anemia at 7.5%, Platelet count decreased at 7.5%, Diarrhea at 5.5%, Palmar-plantar erythrodysesthesia syndrome at 5.0%, and Neutrophil count decreased at 3.8%. The record does not identify an arm beside each of these terms in the posted list.

These counts and percentages describe reported safety events; they do not by themselves establish that a treatment caused an event or allow a complete comparison of safety. The registry record does not provide further details about event definitions, timing, severity breakdowns, or how deaths relate to the adverse-event categories. They should be read alongside the trial’s stated populations and treatment exposure, not as advice about individual care.

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

The posted results describe estimated 3-year IDFS rates of 42.0% for cisplatin or carboplatin and 49.4% for capecitabine in the primary analysis population. The unadjusted risk-difference interval includes zero, while also allowing differences in either direction. The simple comparison therefore leaves uncertainty about the comparative size and direction of the effect.

This does not show that the two treatments are equivalent. Equivalence requires a defined margin and an analysis designed to evaluate whether differences lie within that margin. Nor does an unadjusted p-value of 0.188 tell readers the probability that either treatment is better. The sponsor’s reported analysis is labelled non-inferiority, but the registry record does not report the margin needed to evaluate that claim.

The estimates also do not establish how outcomes would compare for all people with breast cancer, for patients outside the basal-subtype analysis population, or for Arm A observation. The primary analysis population was limited to the specified patients concurrently randomized to Arms B and C after 6/22/2016. The reported results should be understood within that trial context.

IDFS is a composite time-to-event endpoint that includes recurrence, invasive cancer in the opposite breast, another invasive second cancer, or death. The posted rate does not show the separate contributions of those events. It is an estimate at 3 years, not a complete account of all outcomes over longer follow-up. The registry record does not report component-specific results or additional details sufficient to assess all sources of uncertainty.

These findings are statistical descriptions of a clinical trial record, not individualized medical guidance. They neither recommend a treatment nor establish that a treatment works or does not work. Their meaning depends on the endpoint, analysis population, follow-up, and limitations of the information reported.

18. Why This Trial Matters Statistically

This trial illustrates why the stated analysis population matters as much as the overall enrollment figure. Although enrollment is listed as 415, the primary result concerns basal-subtype patients concurrently randomized to two treatment arms after 6/22/2016. The observation arm is described separately and had closed to accrual earlier. A reader who treats all enrollment as the denominator for the primary comparison would misunderstand the scope of the reported estimate.

It also illustrates the difference between a 3-year rate comparison and a time-to-event analysis. The posted arm rates and recalculated risk difference are accessible summaries, while the sponsor reports a hazard ratio in a non-inferiority analysis. These statistics answer related but non-identical questions. A hazard ratio cannot be substituted for a difference between fixed-time rates, and a simple unadjusted calculation cannot stand in for a full sponsor analysis.

Precision is central to interpretation. The primary risk-difference interval spans zero, and the sponsor’s hazard-ratio interval is broad. A point estimate alone can therefore suggest more certainty than the posted evidence supports. The registry record also omits the non-inferiority margin, original sample-size justification, and full analysis plan, which prevents a complete reconstruction of the trial’s inferential framework.

Finally, the several secondary outcomes show why multiplicity and outcome hierarchy matter. Survival, recurrence, and quality-of-life measures can each add context, but unadjusted findings across multiple outcomes need cautious interpretation. Statistical literacy means distinguishing what the posted evidence estimates from what remains unreported or uncertain.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

Several limitations are specific to interpreting this registry entry. The primary analysis is limited to basal-subtype patients concurrently randomized to Arms B and C after 6/22/2016, rather than every participant enrolled or every listed arm. Arm A observation was closed to accrual 05/16/2016, and the posted primary comparison does not include it.

The primary result is a 3-year Kaplan-Meier estimate with censoring for incomplete follow-up or inadequate disease evaluation. The registry record does not report the number censored, the amount of follow-up available, or sensitivity analyses addressing missing information. It also does not report component-specific results for the events included in the IDFS composite.

The sponsor analysis is identified as non-inferiority, but the registry record does not give the non-inferiority margin, model method, or p-value. This makes it impossible to assess the formal non-inferiority criterion from the entry alone. The unadjusted recalculation is not a substitute for that analysis.

The record does not report the trial’s original sample-size justification, detailed randomization procedures, interim analyses, or full statistical analysis plan. It also does not report a multiplicity adjustment for secondary outcomes. The posted secondary summaries therefore have limited context for confirmatory interpretation. Finally, the choice between cisplatin and carboplatin within Arm B is not explained, and the record does not provide additional detail about that treatment assignment.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Platinum in Treating Patients With Residual Triple-Negative Breast Cancer Following Neoadjuvant Chemotherapy — NCT02445391.
• Registry record last updated 2026-11-02; status last verified 2026-10.
• Results first posted 2022-10-05.
• 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

NCT02445391 is a randomized phase III parallel-group trial sponsored by ECOG-ACRIN Cancer Research Group. It compares cisplatin or carboplatin with capecitabine for residual basal-subtype triple-negative breast cancer following neoadjuvant chemotherapy. The primary endpoint is 3-year invasive disease-free survival in the basal-subtype patients concurrently randomized to Arms B and C after 6/22/2016.

The posted primary estimates are 42.0% for cisplatin or carboplatin and 49.4% for capecitabine. The recalculated unadjusted risk difference is 0.075, with a 95% confidence interval from -0.036 to 0.186. The sponsor reports a non-inferiority analysis with a hazard ratio of 1.06 and a 95% confidence interval from 0.62 to 1.81, but the non-inferiority margin is not reported.

Secondary outcomes address recurrence-free survival, overall survival, and quality of life. Interpretation is limited by uncertainty in the primary comparison and missing details on the original design assumptions, full analysis plan, multiplicity handling, and non-inferiority criterion.