Neoadjuvant Study of Two Platinum Regimens in Triple Negative Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Neoadjuvant Study of Two Platinum Regimens in Triple Negative Breast Cancer (NCT02413320), a randomized phase 2 study. The primary outcome is Number of Participants With Pathological Complete Response.

2. Clinical Question

The trial asks whether two chemotherapy strategies that both include carboplatin are associated with different pathological complete response rates before surgery. The distinction is not simply between carboplatin and no carboplatin: both groups received carboplatin, while the accompanying taxane regimen and subsequent treatment differed. One group received carboplatin with paclitaxel and then doxorubicin with cyclophosphamide; the other received carboplatin with docetaxel.

Pathological complete response is defined in the registry record as no evidence of disease in the breast and axilla at pathology review, except for ductal carcinoma in situ. The primary outcome counts participants meeting that definition. Its timeframe is 20 weeks. The clinical question is therefore about a treatment response assessed by pathology, rather than a longer-term outcome such as recurrence or survival.

The registry describes a randomized, open-label phase II trial. The posted primary comparison reports 26.0 participants with the outcome among 48.0 in the paclitaxel-then-doxorubicin-and-cyclophosphamide group and 28.0 among 52.0 in the docetaxel group. The central statistical issue is how precisely those observed counts distinguish the response rates, not whether either regimen should be selected for an individual patient.

3. Trial Design

The registry record describes NCT02413320 as a randomized, open-label, parallel-group phase II trial. Its title identifies a neoadjuvant study of two platinum regimens in triple-negative breast cancer. The recorded enrollment is 101. The study is marked completed, with a start date of 2015-07 and a primary completion date of 2019-02-01.

Participants were assigned to one of two treatment strategies. The first combined carboplatin and paclitaxel, followed by doxorubicin and cyclophosphamide. The recorded regimen specifies paclitaxel 80mg/m2 intravenously every week for 12 weeks, carboplatin AUC 6 intravenously every 21 days for 4 cycles, and then doxorubicin 60mg/m2 and cyclophosphamide 600mg/m2 intravenously every 14 days for 4 cycles. The second strategy combined carboplatin AUC 6 and docetaxel 75mg/m2 intravenously every 21 days for 6 cycles.

Open-label means the registry records no masking. Randomization is intended, in general, to reduce systematic differences between treatment groups at assignment; it does not guarantee that every characteristic will be balanced in a particular trial. The parallel design means the assigned groups received their respective strategies rather than switching between them as part of the stated comparison.

The primary outcome is the number of participants with pathological complete response, assessed at 20 weeks, and the registry names the intention-to-treat population for that outcome. The posted count is 26.0 of 48.0 for the paclitaxel-based strategy and 28.0 of 52.0 for the docetaxel strategy. The registry also lists minimal residual disease as a secondary outcome. The original statistical design details—including the trial's own sample-size justification and planned analysis methods—are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intention-to-treat

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: Intention-to-treat

6. Primary Endpoint

The registry lists the primary outcome as Number of Participants With Pathological Complete Response, measured over 20 weeks.

The primary endpoint counts participants with pathological complete response at the 20-week timeframe. The registry definition is no evidence of disease in the breast and axilla at pathology review, with ductal carcinoma in situ excepted. In other words, the endpoint is based on the pathology assessment of the breast and axilla after neoadjuvant treatment, rather than on a symptom report or an imaging measure.

A pathological response endpoint can be useful in a neoadjuvant study because it records the amount of disease remaining at the time of pathology review. The count-based form also permits a direct comparison of the proportion of participants meeting the definition in each randomized group. This is a general explanation of the endpoint's statistical role, not a claim that it fully captures long-term clinical outcomes.

The stated analysis population is intention-to-treat. In general, an intention-to-treat approach aims to analyze participants according to their randomized assignment, which helps preserve the comparison created by randomization. The registry record does not describe how missing or unevaluable pathology results were handled. The primary outcome is not a time-to-event measure, and the posted result does not by itself describe recurrence, survival, or other outcomes beyond the specified pathology assessment.

7. Results Posted in the Registry

• Carboplatin + Docetaxel: 53.8% (28/52) versus 54.2% (26/48) on control; risk difference -0.3 percentage points (95% CI -19.9 to 19.2), risk ratio 0.99 (0.69–1.43); unadjusted two-proportion z-test p = 0.974.

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.

Number of Participants With Minimal Residual Disease

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Carboplatin + Docetaxel: 67.3% (35/52) versus 67.4% (31/46) on control; risk difference -0.1 percentage points (95% CI -18.7 to 18.5), risk ratio 1.00 (0.76–1.32); unadjusted two-proportion z-test p = 0.993.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Carboplatin + Docetaxel and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists minimal residual disease as the secondary outcome, also assessed at 20 weeks. Its posted comparison follows the same broad pattern as the primary outcome: the group estimates are close, and the comparison does not provide evidence of a clear separation between the assigned strategies. This broad agreement means the secondary finding does not overturn the primary result's central message of a near-zero estimate with uncertainty.

The secondary outcome is related to the primary question because both are pathology-based counts recorded at the same timeframe. They are nevertheless distinct measures. A secondary outcome should not be treated as a substitute for the defined primary endpoint, and a similar pattern across outcomes does not establish that the treatment strategies have identical effects. Each measure may have different definitions, evaluable populations, and uncertainty.

In general, secondary outcomes can help describe a study more fully, but they often carry less evidential weight than a prespecified primary outcome. Testing multiple outcomes increases the chance that at least one result may appear noteworthy by chance if no adjustment or prioritization strategy is used. The registry record does not report a multiplicity adjustment or a complete planned hierarchy for interpreting outcomes. Consequently, the secondary result is best viewed as supporting context rather than independent confirmation of a definitive treatment effect.

The registry lists no reported analyses for the secondary outcome. Its posted summary therefore does not establish what modeling choices, if any, were planned beyond the count comparison. The secondary result may be considered alongside the primary result, but it cannot resolve limitations in the primary estimate's precision or the missing details about analysis and missing-data handling.

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

• Number of Participants With Minimal Residual Disease

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either meets the registry definition of pathological complete response or does not. For this kind of outcome, the posted arm counts can be expressed as response rates, and a risk difference compares those rates by subtraction. In the posted comparison, the contrast is oriented as carboplatin plus docetaxel relative to carboplatin plus paclitaxel followed by doxorubicin plus cyclophosphamide. A negative risk difference therefore indicates a slightly lower observed rate in the docetaxel group, while a positive value would indicate a higher observed rate in that group.

What does the risk difference tell us?

In general, a risk difference describes an absolute separation between two event probabilities. It is often straightforward to interpret because it stays on the probability scale. The posted estimate is -0.003. That value is close to zero, so the observed groups had very similar response rates. It is an estimate from the observed participants, not a known value for all people who might receive either strategy.

The reported confidence interval for the risk difference runs from -0.199 to 0.192. In general, a confidence interval describes the range of estimates reasonably compatible with the data and the method used to construct the interval. A confidence interval is not a guarantee that the true effect lies within the particular interval, and it is not a range of individual participant outcomes. Here the interval contains zero, so the data do not rule out no difference. Its breadth also means the data do not rule out a sizeable difference in either direction.

How should the p-value be read?

The unadjusted p-value is 0.974. In general, a p-value describes how unusual a result at least as far from the null as the observed result would be if the null model and the test assumptions were correct. It is not the probability that the null hypothesis is true, and it does not measure the probability that the observed finding will replicate. The high value is consistent with the estimate being close to zero, but it does not prove that the groups are equivalent.

“Unadjusted” indicates that the posted p-value is not presented as adjusted for multiple comparisons. The registry record does not report a multiplicity strategy or a statistical analysis plan, so the interpretation should not presume that an adjustment was planned or performed. A p-value should also not replace consideration of the effect estimate, confidence interval, outcome definition, and study design.

Why are risk ratios and odds ratios also listed?

The risk ratio compares the response probabilities as a ratio, and the odds ratio compares the corresponding odds. In general, these relative measures can help describe an effect from a different scale, but they can be less directly intuitive than an absolute risk difference. The posted risk ratio is 0.994, with a confidence interval from 0.692 to 1.428. The posted odds ratio is 0.987, with a confidence interval from 0.449 to 2.169. Their point estimates are close to the no-difference value of one, while both intervals include values below and above one. These measures therefore do not provide a more decisive conclusion than the risk difference.

The intervals for different measures are not interchangeable: the risk difference is on an absolute scale, while the risk ratio and odds ratio are relative scales. The interpretation should keep each estimate attached to its measure and interval. The estimates do not describe an adjusted comparison, because an adjusted model is not reported in the registry record.

What does intention-to-treat mean in general?

The primary outcome names the intention-to-treat population. In general, this means participants are analyzed according to their randomized assignment, even if their treatment exposure differs from the assigned strategy. Such an approach can preserve the benefits of random assignment for the comparison. The registry record does not explain whether the posted counts include every randomized participant, how missing pathology assessments were handled, or whether any departures from the stated population occurred. The primary group counts are 48.0 and 52.0; no further reconciliation is documented.

For a binary endpoint, missing outcome data matter because a participant without an evaluable pathology result cannot automatically be classified as having or not having the response. Different handling choices can affect estimated rates and uncertainty. The record does not report imputation, a missing-data sensitivity analysis, or a rule for classifying unevaluable cases. This is a limitation in the available reporting, not evidence that a particular method was or was not used.

What can planning calculations establish?

General sample-size calculations ask how many participants would be needed to have a specified probability of detecting an effect of a chosen size under stated assumptions. The planning illustrations accompanying the posted results are based on the observed effect and specified assumptions; they are not the trial's own original design calculations. Their very large values reflect that the observed effect is close to zero: detecting a very small assumed difference with a conventional design can require a large sample. Such calculations do not establish that a future study should use that effect assumption or that the true effect is exactly the observed estimate.

The registry record does not report the trial's original sample-size justification, planned interim analyses, or a full statistical analysis plan. The posted comparison is therefore best interpreted on its own terms: a near-zero point estimate with a broad interval, from an unadjusted comparison of the observed binary outcome counts.

11. Confidence Intervals and Precision

The point estimate for the primary risk difference is -0.003, and its confidence interval extends from -0.199 to 0.192. The estimate is close to no difference, but the interval is broad relative to that point estimate. It contains zero and values on both sides, so the data are compatible with no difference and with a range of differences favoring either group.

In general, a confidence interval conveys sampling uncertainty under the method used to calculate it. A narrower interval would indicate greater precision, while a wider interval indicates that the observed data leave more uncertainty about the effect size. The interval does not mean that every value within it is equally plausible, and it does not include uncertainty about all possible sources of bias or limitations in outcome measurement.

The alternative measures reinforce the same caution. The risk ratio is 0.994, with an interval from 0.692 to 1.428, and the odds ratio is 0.987, with an interval from 0.449 to 2.169. Both point estimates are close to their no-difference values, but their intervals extend in both directions. The primary result therefore supports neither a precise claim of benefit for one regimen nor a conclusion of equivalence.

The registry record does not report a clinically justified threshold for a meaningful difference. Without such a threshold, statistical precision cannot be translated into a claim that the interval excludes differences important to patients or clinicians. The practical reading is that the observed rates were similar, while the estimate remains too uncertain to resolve the size or direction of any underlying difference with confidence.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total event counts. This is a binary-outcome comparison, and the listed planning values refer to participants in each treatment group. In general, the power columns describe the chance of detecting an assumed difference if that difference is real and the calculation assumptions hold: 80% power and 90% power represent two different target probabilities for detecting the specified effect.

The 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 specified as a fraction of the observed effect. The registry record does not report the trial's original sample-size assumptions or justification; these planning illustrations are not a reconstruction of the original design.

The entries consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. The calculations show that smaller assumed effects require more participants per arm to reach either power target. Since the observed effect is close to zero, using it directly as the target effect produces especially large planning requirements. These values should be understood as illustrations of the consequences of the selected assumptions, not as a forecast of a future study's results.

A planning curve of this kind represents how the required number of participants changes as the target effect changes. Moving toward smaller effects generally raises the required sample size; choosing a larger effect makes the calculation require fewer participants, but does not make that larger effect more likely to be true. The figures are not observed power. They are prospective planning illustrations based on the observed effect and the stated assumptions.

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 = 0.542; treatment proportion p₁ = 0.538; average p̄ = 0.540.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7048 = 1.3814.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.7048 = 0.5932.
4. n = (1.3814 + 0.5932)² / (-0.0032)² = 379,566.7, rounded up to 379,567 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 <- 0.541666666666667                          # control proportion
p1 <- 0.538461538461538                          # 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(2413320)
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 = 379,567 (80% power), 508,132 (90% power)
 75% of observed effect: n per arm = 674,699 (80% power), 903,230 (90% power)
 50% of observed effect: n per arm = 1,517,875 (80% power), 2,032,003 (90% power)
power.prop.test: 379566.7 
Simulated power at n = 379,567 per arm: 0.801 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several hypotheses or outcomes are assessed. In general, the more comparisons that are made, the greater the chance of at least one apparently unusual result arising by chance if no adjustment or prespecified interpretation strategy is used. The registry lists a primary outcome and a secondary outcome, but the registry record does not report a multiplicity adjustment, a hierarchy for testing outcomes, or a full statistical analysis plan. The posted p-value is unadjusted. It should therefore be read as an unadjusted result, not as an estimate of evidence after accounting for all possible analyses.

The registry record lists no reported analyses for the outcome measures. It does not report interim analyses, a stopping rule, or a planned approach to subgroup analyses. These details are not reported in the registry record, so no assumption should be made about whether such procedures were used.

The primary endpoint names the intention-to-treat population, which is a useful statement of the intended analysis population. In general, intention-to-treat analysis retains participants in their randomized groups and helps preserve the randomized comparison. However, the registry does not explain how this population was implemented for participants without an evaluable pathology assessment. The primary counts are 26.0 of 48.0 and 28.0 of 52.0, but the registry does not state the reasons for any difference between these denominators and other enrollment figures.

For the secondary endpoint, the posted denominators are 46.0 and 52.0. The reason for the smaller denominator in one group relative to its primary-outcome denominator is not reported in the registry record. It is not possible from the posted information to determine whether this reflects missing data, endpoint eligibility, or another reason. The record does not describe imputation, exclusion rules, sensitivity analyses for missing data, or how unevaluable outcomes were classified.

These reporting gaps limit assessment of how robust the comparisons are to analysis choices. They do not demonstrate that the results are biased, but they prevent a reader from checking the impact of missing outcomes or understanding the complete planned approach to multiple endpoints.

15. 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 0% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events among 48 participants at risk in the carboplatin-plus-paclitaxel-then-doxorubicin-plus-cyclophosphamide group and zero among 52 participants at risk in the carboplatin-plus-docetaxel group. It also reports zero deaths in each group. These are the recorded counts; they should not be interpreted as proof that serious events or deaths are impossible with either treatment strategy.

For other adverse events, the registry reports 41 affected participants among 48 at risk in the first group and 13 among 52 at risk in the docetaxel group. These figures describe participants with reported other adverse events, not the number or severity of individual events. The registry record does not provide further details about event types, severity, duration, or attribution.

No serious adverse-event terms are listed. Specific serious-event descriptions are therefore not reported in the registry record. Differences in observed adverse-event counts should be interpreted cautiously without fuller information about definitions, ascertainment, exposure, and reporting. These registry figures alone do not provide a complete comparison of safety.

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

The posted primary result shows very similar observed pathological complete response rates in the two randomized groups. The risk difference is -0.003, and the unadjusted p-value is 0.974. These findings do not provide evidence of a statistically detectable difference in this comparison. They do not establish that the regimens are equivalent, because the confidence interval from -0.199 to 0.192 remains compatible with differences in either direction.

The result is specific to the endpoint as defined: no evidence of disease in the breast and axilla at pathology review, except for ductal carcinoma in situ, at the 20-week timeframe. It does not directly answer questions about recurrence, survival, symptoms, or other outcomes. Nor does a response count by itself describe the balance of benefits and harms across all aspects of treatment.

In general, a randomized comparison can help estimate differences between assigned treatment strategies, but interpretation still depends on the quality of outcome ascertainment, completeness of follow-up, and analysis choices. The registry record identifies the primary population as intention-to-treat but does not report the approach to missing pathology assessments or a full statistical analysis plan. Those omissions constrain how completely the posted estimate can be evaluated.

The result should not be read as a treatment recommendation. It does not show that one regimen should be preferred, and it does not demonstrate that either regimen has no effect. It describes the observed response counts and an uncertain between-group comparison in this trial. The appropriate conclusion is limited: the point estimate is close to no difference, while the available precision does not resolve whether a clinically important difference exists.

17. Why This Trial Matters Statistically

This trial is statistically informative because it compares two active, carboplatin-containing neoadjuvant strategies in a randomized design rather than contrasting treatment with no treatment. The clinical question is therefore about the relative response associated with different accompanying chemotherapy regimens and sequences. Describing the comparison accurately matters: the treatment groups differ in more than a single drug, so the result applies to the strategies as assigned, not to an isolated component.

The primary outcome is pathology-based and has a clear registry definition. Its binary form makes the observed group counts interpretable, and the risk difference provides an absolute comparison. The nearly zero point estimate is easy to notice, but the broad confidence interval is equally important. Together, they illustrate why a non-significant test is not the same as evidence of equivalence or proof that meaningful differences are absent.

The record also demonstrates why statistical interpretation depends on reporting beyond a p-value. Information about missing outcomes, multiplicity, interim analyses, and the original sample-size rationale is not reported in the registry record. Without those details, readers can describe the posted result and its uncertainty but cannot fully assess all analysis decisions.

Finally, the planning illustrations show how sample-size requirements depend on the effect chosen for detection. When the observed effect is close to zero, planning to detect a fraction of that effect entails very large participant requirements. These are planning calculations rather than evidence that the original trial was designed around those assumptions. The distinction between observed results, uncertainty, and future-study planning is central to a careful reading of this record.

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.

The primary comparison is imprecise. Although the estimated risk difference is close to zero, its confidence interval extends in both directions and does not establish equivalence. The registry record does not report a clinical margin for a difference considered unimportant, so the result cannot be interpreted against a stated equivalence or non-inferiority threshold.

The record does not report the trial's original sample-size justification, full statistical analysis plan, or interim-analysis procedures. It also does not describe any adjustment for multiple comparisons. These gaps make it difficult to assess the intended analysis framework and the extent to which the posted unadjusted comparison reflects all planned analyses.

The primary endpoint specifies an intention-to-treat population, but missing-data methods and the handling of unevaluable pathology assessments are not reported in the registry record. The secondary outcome has different denominators from the primary outcome in one group, and the reason is not reported. No explanation should be inferred from that difference alone.

The trial is open-label, as recorded in the registry, and the posted information does not describe safeguards or procedures for pathology assessment. Open-label status is a design feature, not by itself proof of biased outcome assessment. The record also provides limited detail for interpreting adverse events: serious-event counts are zero, but specific serious-event terms are not listed, while the other adverse-event counts are not accompanied by further event descriptions in the registry record.

The primary result concerns one pathology-based endpoint at 20 weeks. It does not provide evidence about longer-term outcomes. These limitations narrow the conclusions that can be drawn from the registry record, without negating the descriptive value of the randomized comparison.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Neoadjuvant Study of Two Platinum Regimens in Triple Negative Breast Cancer — NCT02413320.
• Registry record last updated 2021-05-10; status last verified 2021-05.
• Results first posted 2021-04-30.
• 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

NCT02413320 is a completed randomized, open-label phase II trial of two neoadjuvant carboplatin-containing regimens for stage I–III triple-negative breast cancer. The primary outcome is pathological complete response at 20 weeks, defined as no evidence of disease in the breast and axilla at pathology review except for ductal carcinoma in situ.

The posted primary counts are 26.0 of 48.0 in the carboplatin-plus-paclitaxel-then-doxorubicin-plus-cyclophosphamide group and 28.0 of 52.0 in the carboplatin-plus-docetaxel group. The risk difference is -0.003, with a confidence interval from -0.199 to 0.192 and an unadjusted p-value of 0.974. The estimate is close to zero, but the interval leaves substantial uncertainty about the magnitude and direction of a difference.

The registry also lists minimal residual disease as a secondary outcome. Details about the original sample-size rationale, missing-data handling, multiplicity, and full statistical methods are not reported in the registry record. The posted findings describe the observed outcomes and should not be taken as proof of equivalence or as a treatment recommendation.