NeoPHOEBE: Neoadjuvant Trastuzumab + BKM120 in Combination With Weekly Paclitaxel in HER2-positive Primary Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for NeoPHOEBE: Neoadjuvant Trastuzumab + BKM120 in Combination With Weekly Paclitaxel in HER2-positive Primary Breast Cancer (NCT01816594), a randomized phase 2 study. The primary outcome is Pathological Complete Response (pCR) Rate at the Time of Surgery - All Participants.

2. Clinical Question

3. Trial Design

NeoPHOEBE was a randomized, parallel-cohort, two-stage, double-blind, placebo-controlled phase II study. The registry describes triple masking. Participants were assigned to BKM120 with trastuzumab and paclitaxel or to BKM120 placebo with trastuzumab and paclitaxel. The study concerned HER2-positive primary breast cancer before surgery, including PIK3CA wild-type and mutant disease.

The registry lists enrollment of 50 and reports 25 participants in each arm for the primary endpoint. The study status is completed. Its recorded start date is 2013-09-03 and its primary completion date is 2015-02-18. The record identifies Novartis Pharmaceuticals as sponsor.

The primary endpoint was pathological complete response at surgery in all participants. The endpoint description specifies the NSABP definition, based on absence of invasive disease in the breast (ypT0); non-invasive in situ disease could remain in the breast specimen. Nodal histology was not part of this definition. The primary analysis population was the pooled intent-to-treat/full analysis set: participants assigned treatment by randomization. Those randomized but not starting study treatment were considered treatment failures.

The registry lists 16 outcome measures and 16 analyses, including clinical response, breast-conserving surgery, and residual-disease outcomes. The reported secondary outcomes include all-participant and genotype-specific response measures. The record does not report the trial’s original sample-size justification, detailed stage-specific decision rules, or a complete statistical analysis plan. Those elements should not be inferred from the study’s two-stage description.

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: Screened: 68 patients Randomized and analyzed (safety and efficacy): 50 patients

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat set (ITT)/full analysis set (FAS) (pooled): The full analysis set comprised all patients to whom study treatment had been assigned by randomization. Patients who were randomized but did not start study treatment were not replaced and were considered as treatment failures similarly to other patients with no pCR assessment.

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 (N=50) were included in the intention-to-treat set and in the safety analysis set, since all patients started study treatment. Intent-to-treat set (ITT)/full analysis set (FAS) (pooled): The full analysis set comprised all patients to whom study treatment had been assigned by randomization.

6. Primary Endpoint

The registry lists the primary outcome as Pathological Complete Response (pCR) Rate at the Time of Surgery - All Participants, measured over After 6 weeks.

The primary endpoint is the proportion of participants with pathological complete response at surgery. In the registry description, pCR follows NSABP criteria: absence of invasive disease in the breast, expressed as ypT0. A specimen may contain non-invasive in situ cancer and still meet the stated definition. Histological nodal status is not used to define pCR in this endpoint.

Pathological response is assessed in tissue removed at surgery, so it provides a direct measure of residual disease in the breast after neoadjuvant treatment. It differs from a clinical response assessment, which evaluates change in the tumour before surgery. The registry’s primary outcome is reported for all participants rather than as separate primary outcomes for PIK3CA wild-type and mutant groups.

The endpoint is presented as a percentage of participants and accompanied by a 95% confidence interval. Its interpretation depends on the stated breast-only definition: it should not be read as requiring absence of disease in lymph nodes. Nor should it be confused with other residual-disease definitions listed among the secondary outcomes, which refer to breast and lymph-node findings and include different criteria.

For the primary endpoint, the reported proportions were 32.0% with BKM120 and 40.0% with placebo. These estimates describe the observed groups in this trial; they do not by themselves establish a reliable difference between regimens.

7. Results Posted in the Registry

• Trastuzumab + BKM120 PBO + Paclitaxel: 40.0% (10/25) versus 32.0% (8/25) on control; risk difference 8.0 percentage points (95% CI -18.5 to 34.5), risk ratio 1.25 (0.59–2.64); unadjusted two-proportion z-test p = 0.556.

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.

Overall Objective Clinical Response Rate at the End of the Biologic Window (After Week 6) Compared to Baseline (Key Secondary) - All Participants

• 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:
  • Trastuzumab + BKM120 PBO + Paclitaxel: 44.0% (11/25) versus 56.0% (14/25) on control; risk difference -12.0 percentage points (95% CI -39.5 to 15.5), risk ratio 0.79 (0.45–1.38); unadjusted two-proportion z-test p = 0.396.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Trastuzumab + BKM120 PBO + Paclitaxel and the control. The interval gives the range of effects that remain compatible with the data.

Overall Objective Clinical Response Rate at the End of the Biologic Window (After Week 6) Compared to Baseline (Key Secondary) - PIK3A Wild Type Participants

• 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:
  • Trastuzumab + BKM120 PBO + Paclitaxel: 42.9% (9/21) versus 61.9% (13/21) on control; risk difference -19.0 percentage points (95% CI -48.7 to 10.6), risk ratio 0.69 (0.38–1.26); unadjusted two-proportion z-test p = 0.217.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Trastuzumab + BKM120 PBO + Paclitaxel and the control. The interval gives the range of effects that remain compatible with the data.

Rate of Breast Conserving Surgery (Most Radical Surgery)

• 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:
  • Trastuzumab + BKM120 PBO + Paclitaxel: 68.0% (17/25) versus 60.0% (15/25) on control; risk difference 8.0 percentage points (95% CI -18.5 to 34.5), risk ratio 1.13 (0.75–1.72); unadjusted two-proportion z-test p = 0.556.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Trastuzumab + BKM120 PBO + Paclitaxel and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover clinical response, breast-conserving surgery, residual-disease definitions, overall response before surgery, and response by hormone-receptor status, among other listed measures. The registry lists 13 posted secondary outcomes. The results described in the record do not point uniformly in one direction: clinical response estimates favor the BKM120 arm, while the breast-conserving surgery estimate is higher in the placebo arm. These outcomes assess different aspects of treatment and should not be treated as interchangeable measures of the primary pathological endpoint.

The all-participant clinical response outcome and the wild-type subgroup outcome are related to tumour response during the biologic window, whereas pCR is assessed at surgery using a tissue-based definition. A clinical response does not establish pCR, and a surgical outcome such as breast-conserving surgery is not itself a measure of pathological eradication. The secondary findings therefore add context but do not override the primary comparison.

Multiple secondary outcomes create multiple opportunities to observe an apparently notable result by chance. The record does not report a multiplicity adjustment or a hierarchy for interpreting the secondary tests. Unless such control is documented, secondary p-values should be treated as exploratory and carry less weight than the prespecified primary endpoint. Subgroup results require additional caution because they concern narrower populations and may be less precise.

The posted registry detail does not include results for every listed secondary outcome in the information summarized for this analysis; those endpoint-specific results are not reported in the registry record. The available pattern should consequently be read as an incomplete view of a broad outcome set, not as a comprehensive or confirmatory synthesis.

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

• Overall Objective Clinical Response Rate at the End of the Biologic Window (After Week 6) Compared to Baseline (Key Secondary) - All Participants
• Overall Objective Clinical Response Rate at the End of the Biologic Window (After Week 6) Compared to Baseline (Key Secondary) - PIK3A Wild Type Participants
• Overall Objective Clinical Response Rate at the End of the Biologic Window (After Week 6) Compared to Baseline (Key Secondary) - PIK3A Mutant Participants
• Rate of Breast Conserving Surgery (Most Radical Surgery)
• Percentage of Participants With No Invasive and Non-invasive (DCIS) Residuals in Breast and Lymph Nodes Per GBG Definition
• Percentage of Participants With No Invasive and Non-invasive (DCIS) Residuals in Breast and Lymph Nodes Per MD Anderson Definition
• Overall Objective Response Rate (ORR) Prior to Surgery for All Participants
• Percentage of Participants With pCR Rates by Hormone Receptor Status - Positive Estrogen Receptor (ER+)

9. Statistical Interpretation

10. Statistical Methods Explained

For a binary endpoint such as pCR, each participant either meets the defined response criterion or does not. The reported percentage describes the fraction of participants meeting that criterion in an arm. It is a group-level estimate, not a prediction for an individual. Here, the primary endpoint uses the registry’s breast-tissue definition; it is not interchangeable with clinical response or with residual-disease definitions that also consider lymph nodes.

What does the risk difference express?

A risk difference subtracts one arm’s event proportion from the other on the proportion scale. The posted recalculation expresses the placebo-minus-BKM120 contrast as 0.08. A value of zero corresponds to equal observed proportions. The direction depends on the order of the arms, so it is important to identify which regimen is first and which is second when reading a contrast. A risk difference is an absolute comparison, unlike a relative risk or odds ratio.

How should the confidence interval be read?

A confidence interval describes uncertainty around an estimated quantity under the method used to construct it. In repeated use of a valid procedure, intervals would cover the underlying quantity at the stated rate. For a reader, the practical point is that the interval shows a range of values compatible with the data and method, rather than a guarantee that the true value lies within a particular interval. For the arm-specific response proportions, the 95% intervals are broad. The recalculated contrast interval includes zero, so the data do not precisely distinguish a positive difference from a negative one.

What does the Fisher exact test assess?

The sponsor-reported primary analysis uses Fisher exact testing. This test evaluates evidence against a null association between randomized group and a binary outcome, using the observed group counts. It is commonly used for categorical comparisons, particularly when group counts are limited. A p-value describes how unusual data at least as incompatible with the null would be if that null model and test assumptions held. It is not the probability that the null is true, nor a measure of the size or importance of an effect.

The sponsor’s reported Fisher exact p-value is 0.811. The simple unadjusted recalculation from the posted summary statistics gives p = 0.556. The record does not state why these values differ. The reported test and the recalculation should therefore be kept distinct: one is the registry’s sponsor-reported analysis, and the other is a summary-statistic-based reanalysis.

How do relative measures differ?

A relative risk compares event proportions as a ratio. An odds ratio compares the odds of an event between groups. Both can express relative association, but their numerical meaning differs from an absolute risk difference. When events are not rare, an odds ratio should not be read as though it were a risk ratio. Relative measures can also be unstable when event counts are limited. The primary interpretation should therefore consider the endpoint proportions and their uncertainty alongside any relative measure, rather than relying on a single ratio.

Why do small groups matter?

With limited observations, one or a few outcome changes can have a noticeable effect on an estimated proportion. Confidence intervals reflect sampling uncertainty, and small groups commonly yield less precise estimates. Randomization supports a fair comparison in expectation, but does not eliminate imprecision in a particular small trial. A non-significant result in this setting does not demonstrate that the regimens have identical effects.

More generally, over-dispersion arises when observed variability exceeds what a statistical model assumes. For binary outcomes, this can occur when observations are more heterogeneous than a simple model allows. Appropriate methods and design details depend on the outcome structure and analysis plan; the registry record does not report an over-dispersion model for this endpoint, so none should be presumed.

Finally, the primary population definition matters. The registry describes the intent-to-treat/full analysis set as everyone assigned treatment by randomization and says randomized participants who did not start treatment were counted as treatment failures. This preserves assignment as the basis of comparison, rather than comparing only people who completed treatment. The record does not provide enough detail to infer additional rules for other missing observations or protocol deviations.

11. Confidence Intervals and Precision

The pCR estimate is 32.0% in the BKM120 arm, with a 95% confidence interval of 14.9% to 53.5%. In the placebo arm it is 40.0%, with a 95% confidence interval of 21.1% to 61.3%. These intervals show that each arm’s response proportion is estimated with considerable uncertainty. The ranges overlap, and the recalculated interval for the between-arm contrast includes no difference.

Overlap between two separate arm-specific confidence intervals is not itself a formal test of the contrast. The direct comparison is the more relevant quantity for judging whether the groups differ, because it estimates uncertainty in the difference itself. Even that direct comparison is imprecise in this trial. The recalculated risk difference is 0.08, but its confidence interval extends to both sides of zero.

Precision is distinct from whether a result crosses a conventional significance threshold. A wide interval can include a range of potentially meaningful values while a test remains non-significant. Conversely, a narrow interval can still be centered on a small difference. The primary record’s p-value and the confidence intervals answer related but not identical questions.

These results therefore leave substantial uncertainty about the size and direction of the difference in pCR between regimens. The recorded group sizes and observed event proportions support a description of this trial, but they do not yield a precise estimate that should be treated as definitive.

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 events. They are illustrations based on the observed effect, not the original trial’s design calculation. The registry record does not report the original sample-size justification or its design assumptions.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect used for each illustration is the stated fraction of the observed effect. For the primary endpoint, planning for 100% of the observed effect gives 564 participants per arm for 80% power and 755 participants per arm for 90% power. Planning for 75% of the observed effect gives 991 participants per arm for 80% power and 1,326 participants per arm for 90% power. Planning for 50% of the observed effect gives 2,201 participants per arm for 80% power and 2,946 participants per arm for 90% power.

The 80% power column describes the planned chance of detecting the specified effect under the stated assumptions if that effect is real. The 90% column describes a higher chance of detection for the same assumed effect, and therefore calls for more participants per arm. Smaller effects are harder to distinguish from random variation, so the planning figures rise as the assumed fraction of the observed effect gets smaller.

These calculations are not observed power. They are planning illustrations and should not be interpreted as a retrospective measure of how likely the completed trial was to find a result.

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 = 0.320; treatment proportion p₁ = 0.400; average p̄ = 0.360.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6788 = 1.3305.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6765 = 0.5693.
4. n = (1.3305 + 0.5693)² / (0.0800)² = 563.9, rounded up to 564 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 <- 0.32                          # control proportion
p1 <- 0.4                          # 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(1816594)
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 = 564 (80% power), 755 (90% power)
 75% of observed effect: n per arm = 991 (80% power), 1,326 (90% power)
 50% of observed effect: n per arm = 2,201 (80% power), 2,946 (90% power)
power.prop.test: 563.9 
Simulated power at n = 564 per arm: 0.799 (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 reports a sponsor analysis of the primary comparison using Fisher exact testing, with p = 0.811. It also reports Fisher exact analyses for the secondary outcomes described in the record. The primary result should be understood first as the sponsor-reported inferential analysis, not replaced by a recalculation based on rounded summary statistics.

The unadjusted recalculation from the posted primary arm summaries gives p = 0.556 and a risk difference of 0.08. The two p-values are not the same. The registry record does not report why they differ, nor does it provide enough detail to reconstruct the sponsor’s full analysis. Rounded percentages, analysis populations, or other analytic details should not be asserted as the explanation without documentation.

The recalculated quantities are useful as a transparent check of the posted summaries, but they are not a substitute for the sponsor’s analysis or a new analysis of participant-level data. The record marks no discrepancy. The appropriate reading is to keep the methods and results clearly labelled: sponsor-reported Fisher exact result on one hand, and simple unadjusted summary-statistic recalculation on the other.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, subgroups, or comparisons are tested. Even if each test is conducted at a conventional error rate, the chance of at least one chance-positive finding can increase as more tests are considered. This matters in NeoPHOEBE because the registry lists 16 outcome measures and 16 analyses, including multiple secondary outcomes and genotype-specific response measures.

The primary endpoint provides the clearest single comparison, but the record does not report whether secondary tests were adjusted for multiplicity, whether a formal testing hierarchy was used, or how the two-stage design affected inference. These details are not reported in the registry record. Without them, secondary p-values should not be interpreted as if each were an isolated confirmatory test.

The registry defines the primary analysis population as the pooled intent-to-treat/full analysis set, comprising participants assigned treatment at randomization. It says participants who were randomized but did not start treatment were not replaced and were considered treatment failures. This is relevant to interpretation because it retains randomized assignment as the basis for the primary comparison.

Other missing-data procedures are not reported in the registry record. In particular, the available description does not establish how every other missing endpoint assessment, withdrawal, or protocol deviation was handled. Nor does it state whether sensitivity analyses were performed. These omissions limit the ability to assess how robust the endpoint estimates are to missing observations.

The record’s description of a two-stage study does not by itself reveal the stage-specific hypotheses, stopping boundaries, interim looks, or any adjustment for repeated testing. Those details are not reported in the registry record, so the two-stage label should not be used to infer an interim-analysis plan. The original sample-size justification and full statistical analysis plan are also not reported. These gaps are important when judging how exploratory findings relate to the primary result.

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: hepatic enzyme increased (8.0%), diarrhoea (4.0%), catheter site pain (4.0%), pyrexia (4.0%), thrombosis in device (4.0%).

The registry reports serious adverse events in 8 participants in the BKM120 arm and 2 participants in the placebo arm; each arm lists 25 participants at risk. It reports other adverse events affecting 21 participants in the BKM120 arm and 19 in the placebo arm, with 25 at risk in each. No deaths are reported in either arm.

These are counts of affected participants, not a complete description of event duration, severity distribution, timing, or causal attribution. A participant may experience more than one event, so participant counts should not be read as event totals. The registry lists hepatic enzyme increased at 8.0% among the top serious terms, along with diarrhoea, catheter site pain, pyrexia, thrombosis in device, and hepatotoxicity at 4.0% each. The record detail does not assign those terms to a specific arm.

Safety comparisons from a study of this size are descriptive and uncertain. The counts do not by themselves establish that one regimen caused more or fewer adverse events, and they should be interpreted alongside the trial’s limited size and the registry’s incomplete event-level detail.

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

The result describes what was observed in this randomized phase II study: pCR was recorded in 32.0% of the BKM120 arm and 40.0% of the placebo arm, with broad confidence intervals. The sponsor-reported Fisher exact test did not show a statistically clear difference. The estimates do not establish that either regimen is superior, but neither do they establish equivalence or prove that the regimens have the same effect.

The result applies to the registry-defined endpoint and population. The endpoint concerns absence of invasive disease in the breast specimen, while allowing non-invasive in situ disease and not incorporating nodal status. Other outcomes, including clinical response and residual-disease criteria involving lymph nodes, answer different questions.

The trial’s 25 participants per arm for the primary endpoint leave considerable uncertainty. A non-significant result can arise when an effect is absent, when the effect is modest, or when the data are too imprecise to distinguish the effect from chance variation. The trial result alone does not separate these possibilities.

Nor does the primary endpoint resolve longer-term outcomes or establish how the findings apply beyond the population and treatment setting described in the registry. The information summarized for this analysis does not report long-term outcomes or a complete statistical analysis plan. Secondary results may contribute context, but their multiplicity and differing definitions make them unsuitable as a substitute for the primary comparison.

Accordingly, the appropriate conclusion is limited: the registry reports a small randomized comparison with uncertain pCR estimates and no clear statistical evidence of a difference on the primary endpoint. It does not support a broader claim that either regimen works or does not work.

18. Why This Trial Matters Statistically

This trial illustrates why an observed difference and a statistically persuasive difference are not the same thing. The arm-specific pCR estimates are separated, but the confidence intervals are broad and the recalculated contrast interval crosses zero. The primary comparison therefore calls for attention to uncertainty, not just the ordering of the percentages.

It also shows why endpoint definitions matter. The primary pCR measure uses a breast-only NSABP definition, while several secondary outcomes refer to clinical response or residual disease in breast and lymph nodes. Different definitions can produce different proportions without contradicting one another, because they measure different outcomes.

The trial also highlights the distinction between a sponsor-reported analysis and a transparent recalculation from posted summaries. Both can be described, but they are not interchangeable. Reporting the method, analysis population, and uncertainty helps readers understand what each result can support and where the record leaves questions unanswered.

Finally, a small phase II comparison can be useful for characterizing observed outcomes while still being too imprecise to settle a treatment difference. Planning illustrations based on the observed effect make the scale of future study requirements easier to understand, but they do not replace the original design rationale. The registry does not report that rationale, reinforcing the need to separate recorded evidence from assumptions about how the trial was planned.

19. Limitations

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

The primary analysis includes 25 participants per arm, limiting precision for a binary endpoint. The confidence intervals are broad, and the primary comparison does not tightly estimate the direction or size of a difference. The study is phase II, and the registry record does not report the original sample-size justification, so the intended precision or target effect cannot be assessed from the available record.

The record describes the study as two-stage but does not report stage-specific rules, interim analyses, stopping criteria, or how these design features informed statistical inference. The complete statistical analysis plan and any multiplicity control are not reported. This is particularly relevant given the number of secondary endpoints and subgroup analyses listed.

The registry identifies an intent-to-treat/full analysis set and describes how randomized participants who did not begin treatment were handled. It does not report the full approach to other missing observations, deviations, or sensitivity analyses. Those omissions limit assessment of the robustness of estimates.

The pCR definition is specific to invasive disease in the breast and excludes nodal histology from the definition. Other endpoints use distinct response or residual-disease criteria, so they cannot be treated as direct replications of the primary outcome. Secondary results also have reduced evidential weight when many outcomes are considered without documented multiplicity adjustment.

Finally, the sponsor-reported Fisher exact p-value differs from the simple unadjusted recalculation. The registry does not explain the difference. Without participant-level data and fuller analytic documentation, the recalculation cannot resolve that issue or reproduce the sponsor analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: NeoPHOEBE: Neoadjuvant Trastuzumab + BKM120 in Combination With Weekly Paclitaxel in HER2-positive Primary Breast Cancer — NCT01816594.
• Registry record last updated 2019-11-14; status last verified 2019-10.
• Results first posted 2019-11-14.
• 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

NeoPHOEBE was a completed, randomized, parallel-cohort, double-blind, placebo-controlled phase II study of neoadjuvant BKM120 with trastuzumab and paclitaxel versus placebo with trastuzumab and paclitaxel in HER2-positive primary breast cancer. The registry lists enrollment of 50 and identifies Novartis Pharmaceuticals as sponsor.

The primary outcome was pCR at surgery in all participants, defined by absence of invasive disease in the breast. The observed proportions were 32.0% and 40.0%, with broad 95% confidence intervals. The sponsor-reported Fisher exact result was p = 0.811; a simple unadjusted recalculation gave p = 0.556. The record does not explain the difference.

The registry lists multiple secondary outcomes and safety results. Interpretation is constrained by imprecision, multiplicity, and missing detail on the original design rationale and full analysis plan.