A Study of Taselisib + Fulvestrant Versus Placebo + Fulvestrant in Participants With Advanced or Metastatic Breast Cancer Who Have Disease Recurrence or Progression During or After Aromatase Inhibitor Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Taselisib + Fulvestrant Versus Placebo + Fulvestrant in Participants With Advanced or Metastatic Breast Cancer Who Have Disease Recurrence or Progression During or After Aromatase Inhibitor Therapy (NCT02340221), a randomized phase 3 study. The primary outcome is Progression-Free Survival (PFS) as Assessed by Investigator Using Response Evaluation Criteria in Solid Tumors (RECIST) Version 1.1 (v1.1) at Primary Analysis.

2. Clinical Question

3. Trial Design

This was a phase III, randomized, double-blind, parallel-group, placebo-controlled study sponsored by Hoffmann-La Roche. It enrolled 631 participants overall. The trial compared taselisib plus fulvestrant with placebo plus fulvestrant in postmenopausal women with estrogen receptor-positive and HER2-negative locally advanced or metastatic breast cancer after disease recurrence or progression during or after aromatase inhibitor therapy. The brief summary identifies PIK3CA-mutant disease as a central eligibility and enrollment focus, with enrollment enriched for participants with PIK3CA-mutant tumors through central testing.

The stated allocation was 2:1 in favor of taselisib plus fulvestrant. In the primary endpoint population, 340 participants were in the taselisib plus fulvestrant group and 176 were in the placebo plus fulvestrant group. These endpoint analysis counts should not be mistaken for the overall enrollment: the primary endpoint description specifies randomized participants with PIK3CA-mutant tumors, regardless of whether they received any study treatment.

Both groups received fulvestrant. The experimental group also received oral taselisib, while the comparator group received oral placebo. Fulvestrant was administered by intramuscular injection on Cycle 1, Days 1 and 15, then on Day 1 of subsequent 28-day cycles. The registry describes continuing treatment until disease progression, unacceptable toxicity, or study termination by the sponsor. Double masking and the placebo comparator were intended to keep treatment assignment concealed during the comparison, although the registry record does not report further details about masking procedures.

The primary endpoint was investigator-assessed progression-free survival at the primary analysis. The registry record lists a 15 Oct 2017 data cutoff, approximately 2.5 years after the stated start of follow-up for that analysis. The study status is terminated. The record does not report why the study was terminated, the sponsor’s original sample-size justification, or the protocol’s detailed statistical 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: The study enrolled postmenopausal women with estrogen receptor-positive and human epidermal receptor 2 (HER2)-negative locally advanced or metastatic breast cancer who had disease recurrence or progression during or after aromatase inhibitor therapy. Randomization was stratified by three factors: 1) visceral versus non-visceral disease, 2) sensitivity versus non-sensitivity to most recent endocrine therapy, and 3) geographical region.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Randomized participants with PIK3CA-mutant tumors, regardless of whether they received any amount of study treatment.

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: The intent-to-treat (ITT) population included all randomized participants regardless of whether they received any amount of study treatment.

6. Primary Endpoint

The registry lists the primary outcome as Progression-Free Survival (PFS) as Assessed by Investigator Using Response Evaluation Criteria in Solid Tumors (RECIST) Version 1.1 (v1.1) at Primary Analysis, measured over From randomization until the first occurrence of disease progression or death from any cause, whichever occurs earlier (up to the 15 Oct 2017 data cutoff, approximately 2.5 years).

Progression-free survival is a time-to-event endpoint. In this trial it measured the time from randomization until the investigator identified disease progression using RECIST v1.1, or death from any cause, whichever occurred earlier. Participants without a recorded event by the analysis cutoff contribute information up to the time they were last known to be without progression or death, subject to the analysis procedures; the registry record does not describe those procedures in detail.

The progression definition used several features of tumor assessment. For target lesions, progression required at least a 20% increase in the sum of diameters, relative to the smallest sum on study, including baseline, together with an absolute increase of at least 5 millimeters. Unequivocal progression of existing non-target lesions also counted, as did the appearance of one or more new lesions. These rules make the endpoint more specific than a general impression of worsening disease.

Time-to-event endpoints are useful when the timing of an event matters and participants may have different lengths of follow-up. The median describes the time by which half of the population has experienced the event, as estimated by the analysis; it does not describe every participant’s experience or the average duration. A hazard ratio compares event rates over follow-up under the analysis model, rather than comparing medians directly. Here the registry reports investigator-assessed progression-free survival medians and a hazard ratio with a confidence interval. The endpoint gives a structured comparison of disease progression or death, but it does not by itself describe overall survival, quality of life, or the balance of benefits and harms.

7. Results Posted in the Registry

• Placebo+Fulvestrant vs Taselisib+Fulvestrant: hazard ratio 0.70 (95% CI 0.56–0.89), reported p = 0.004 (as reported in the registry).

8. Secondary Efficacy Endpoints

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

Percentage of Participants With Objective Response (Partial Response [PR] Plus Complete Response [CR]), as Assessed Using RECIST v.1.1 at Primary Analysis

• 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:
  • Taselisib+Fulvestrant: 28.0% (74/264) versus 11.9% (16/134) on control; risk difference 16.1 percentage points (95% CI 8.4 to 23.8), risk ratio 2.35 (1.43–3.87); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Taselisib+Fulvestrant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants With Objective Response (PR Plus CR), as Assessed Using RECIST v.1.1 at Final Analysis

• 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:
  • Taselisib+Fulvestrant: 31.1% (82/264) versus 13.4% (18/134) on control; risk difference 17.6 percentage points (95% CI 9.6 to 25.7), risk ratio 2.31 (1.45–3.68); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Taselisib+Fulvestrant than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Overall Survival (OS) at Primary Analysis

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Placebo+Fulvestrant vs Taselisib+Fulvestrant: hazard ratio 0.85 (95% CI 0.58–1.25), reported p = 0.415 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Placebo+Fulvestrant vs Taselisib+Fulvestrant and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover response, clinical benefit, duration of response, and overall survival, with some outcomes reported at both primary and final analyses. Across the objective-response results, the taselisib plus fulvestrant group has higher posted response percentages than the placebo plus fulvestrant group at both analysis times. The sponsor’s reported comparative analyses also classify the response results as superiority. These endpoints provide evidence about tumor response under RECIST v1.1, but they are not the same measure as progression-free survival.

Overall survival is a distinct endpoint based on death from any cause. At the primary analysis, its reported hazard ratio and confidence interval do not establish a statistically clear difference. This does not erase the primary progression-free survival finding; it means the available endpoints address different outcomes and have different levels of statistical evidence. The final overall-survival result is listed among the secondary outcomes, but the registry record does not provide a posted final overall-survival estimate in the results.

Secondary results are generally less definitive when many outcomes, time points, or comparisons are examined. Testing multiple hypotheses increases the opportunity for apparently notable results to occur by chance unless the analysis plan controls that risk. The registry record lists multiple outcome measures and analyses, but does not report whether or how multiplicity was controlled. Accordingly, secondary p-values should be treated as nominal evidence rather than as confirmatory results with a known family-wise error guarantee. Their interpretation also depends on endpoint definitions, analysis populations, missing data handling, and the sponsor’s analysis methods, some of which are not fully reported in the registry record.

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

• Percentage of Participants With Objective Response (Partial Response [PR] Plus Complete Response [CR]), as Assessed Using RECIST v.1.1 at Primary Analysis
• Percentage of Participants With Objective Response (PR Plus CR), as Assessed Using RECIST v.1.1 at Final Analysis
• Overall Survival (OS) at Primary Analysis
• OS at Final Analysis
• Percentage of Participants With Clinical Benefit, as Assessed According to RECIST v1.1 at Primary Analysis
• Percentage of Participants With Clinical Benefit, as Assessed According to RECIST v1.1 at Final Analysis
• Duration of Objective Response, as Assessed by Investigator Using RECIST v1.1 at Primary Analysis
• Duration of Objective Response, as Assessed by Investigator Using RECIST v1.1 at Final Analysis

9. Statistical Interpretation

10. Statistical Methods Explained

What does a median time-to-event result represent?

A median time-to-event estimate marks the point at which the estimated event-free proportion has reached one half. It is a feature of the estimated follow-up distribution, not an arithmetic average of individual times. Participants who have not experienced progression or death by the cutoff can still contribute follow-up information, but the registry record does not explain the specific censoring rules or methods used to handle incomplete follow-up. The median also does not convey the entire pattern of event timing: different survival curves can share a median and still differ at other points in follow-up.

For the primary endpoint, the registry reports a median of 5.39 months for placebo plus fulvestrant and 7.43 months for taselisib plus fulvestrant. The estimates have their own confidence intervals. Those intervals express uncertainty about each median under the analysis, but they do not directly test the difference between medians. The reported group comparison uses a hazard ratio and a log-rank method instead.

How should a hazard ratio be read?

A hazard is an event rate at a particular time among participants who have not yet experienced the event. A hazard ratio summarizes a relative comparison of those rates over follow-up under the model and assumptions used for the analysis. A value of 1 corresponds to no relative difference in hazards; values on either side indicate different relative event rates according to the comparison’s group ordering. A hazard ratio is not a probability, a difference in median survival, or a direct statement about how long an individual will remain event-free.

The registry reports a hazard ratio of 0.70 for the primary progression-free survival comparison, with a 95% confidence interval of 0.56 to 0.89. The comparison is labeled Placebo+Fulvestrant versus Taselisib+Fulvestrant, while the registry classifies the reported result as superiority. The estimate and its interval should be read in conjunction with the sponsor’s stated group comparison and analysis, rather than recast as a new effect estimate from the medians. The p-value of 0.004 comes from the reported log-rank analysis.

The log-rank test compares event-time distributions across groups, taking account of the timing of events and censored follow-up. It does not use only the medians. Its interpretation depends on the analysis population and the way follow-up and events were handled, details that are not fully described in the registry record.

What does a confidence interval contribute?

A confidence interval describes statistical uncertainty around an estimate under the method used to construct it. A narrower interval indicates greater precision in that estimate than a wider interval, all else being equal. It does not mean that the true value has a specified probability of lying inside the particular interval after the data have been observed. For a hazard ratio, an interval that includes 1 is compatible with no relative difference under the corresponding statistical framework; an interval entirely on one side of 1 is less compatible with that null value. This is one reason to read the interval alongside the point estimate and p-value.

For the primary endpoint, the reported hazard-ratio interval lies below 1. For the overall-survival analysis, the interval is 0.58 to 1.25 and includes 1. The latter is less precise about the direction and size of a relative difference and does not provide a statistically clear result at the reported analysis. Neither interval alone says whether an effect is clinically important.

Why are these results not recalculated from the posted medians?

For time-to-event outcomes, the registry’s stated approach uses the sponsor’s reported hazard ratios. Reconstructing a hazard ratio from the group medians would not be a valid simple recalculation: it would discard event timing, censoring, and other information used by the time-to-event analysis. The sponsor’s reported hazard ratios and log-rank p-values are therefore the relevant comparison statistics presented for progression-free survival and overall survival.

For binary response outcomes, simple unadjusted calculations from posted counts can be displayed as descriptive comparisons, but they are not identical to the sponsor’s Cochran-Mantel-Haenszel odds-ratio analyses. The latter are the sponsor’s reported analyses. The registry record does not describe the strata or adjustment details needed to reproduce those analyses fully. In the absence of a discrepancy flagged in the posted results, the two approaches should be understood as different analyses, not interchangeable estimates.

Why do event definitions and population definitions matter?

Progression-free survival depends on how progression is defined and assessed. RECIST v1.1 supplies explicit rules for target lesions, non-target lesions, and new lesions, while investigator assessment determines when those criteria are met. Death from any cause is also counted as an event. A change in assessment timing or missing tumor evaluation can affect the observed event record; the registry does not provide a detailed account of these processes.

The primary endpoint population is stated as randomized participants with PIK3CA-mutant tumors, regardless of treatment received. The analysis counts of 176 and 340 refer to the two treatment groups for that endpoint, not to all 631 enrolled participants. The registry gives the population definition but does not report a full accounting of exclusions or missing data for each endpoint. This limits independent assessment of how closely the analyzed groups followed the intended population definition.

11. Confidence Intervals and Precision

Precision is reflected in the confidence intervals around the estimates. For primary progression-free survival, the placebo plus fulvestrant median was 5.39 months with a 95% confidence interval of 3.68 to 7.29 months. The taselisib plus fulvestrant median was 7.43 months with a 95% confidence interval of 7.26 to 9.07 months. These intervals quantify uncertainty around each group’s median; they are not a confidence interval for the difference between medians.

The primary hazard ratio was 0.70, with a 95% confidence interval of 0.56 to 0.89. This interval is wholly below 1 and is consistent with the reported superiority classification and p = 0.004. The range still allows for a range of relative effects, so the point estimate should not be treated as exact. The interval describes statistical precision, not clinical importance or individual response.

For overall survival, the group medians were 23.56 months and 26.81 months, while the reported hazard ratio was 0.85, with a 95% confidence interval of 0.58 to 1.25. This interval includes 1 and spans values on either side of it. The result is therefore less conclusive about the direction and size of a relative difference than the primary progression-free survival result.

Response percentages also have confidence intervals, and the intervals provide a sense of the uncertainty around each group’s estimated response percentage. Their widths reflect, among other things, the amount of information available for that outcome. These intervals and the sponsor’s comparative odds-ratio intervals answer related but distinct questions. Precision should be considered with the endpoint definition, analysis population, and multiplicity context, not as a standalone judgment about the quality or importance of a result.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations are based on the observed effect, not on the trial’s own original design assumptions. The trial’s original sample-size justification and design assumptions are not reported in the registry record. The planning calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider effects set at 100%, 75%, and 50% of the observed effect. For binary outcomes, the entries are participants per arm. For time-to-event outcomes, the entries are total events across the study, not participants per arm.

The 80% power column gives the planning number of participants per arm, or total events for a time-to-event endpoint, under which the assumed analysis would have an 80% chance of detecting the specified effect if that effect were the true one and the planning assumptions held. The 90% power column describes the corresponding planning target for a 90% chance. These are probabilities used for prospective planning, not guarantees that a particular study will reach a result.

Each row changes the assumed effect size. A smaller effect is harder to distinguish from random variation, so the planning illustration requires more participants or more events to detect it at the same power and significance level. This is not observed power: it is a planning illustration calculated from the observed effect, not an estimate of the probability that the completed trial detected a true effect.

For the survival analyses, event counts are the relevant planning unit because information accrues through observed events and follow-up, not simply through enrollment. For binary outcomes, the participant-per-arm figures use an equal-allocation planning assumption. Those assumptions differ from the trial’s stated 2:1 allocation. The illustrations are therefore not a reconstruction of the trial’s design or a claim about how the sponsor selected the enrollment target.

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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.700, so ln(HR) = -0.3567.
2. d = 4 × (1.96 + 0.842)² / [ln(0.700)]² = 246.8, rounded up to 247 events in total 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
hr <- 0.7                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(2340221)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 247 (80% power), 331 (90% power)
 75% of observed effect: events = 439 (80% power), 588 (90% power)
 50% of observed effect: events = 988 (80% power), 1,322 (90% power)
Simulated power with 247 events: 0.805 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

14. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 368 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 631 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 5.39          # control-arm median, months (converted from the posted unit)
hr          <- 0.7          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
    Analysis              Value Efficacy
   IA 1: 33%                  Z   3.7103
      N: 230        p (1-sided)   0.0001
 Events: 112       ~HR at bound   0.4947
   Month: 15   P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.7   0.0338
   IA 2: 67%                  Z   2.5114
      N: 366        p (1-sided)   0.0060
 Events: 223       ~HR at bound   0.7140
   Month: 24   P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.7   0.5603
       Final                  Z   1.9930
      N: 368        p (1-sided)   0.0231
 Events: 334       ~HR at bound   0.8039
   Month: 60   P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.7   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

15. Analyses Reported by the Sponsor

The sponsor’s reported primary analysis is the central time-to-event comparison. It reports a log-rank hazard ratio of 0.70 for progression-free survival, with a 95% confidence interval of 0.56 to 0.89 and p = 0.004. The registry record classifies that analysis as superiority. Because time-to-event comparisons depend on event timing and censored follow-up, the hazard ratio is not recalculated from the posted group medians.

For the secondary objective-response outcomes, the sponsor reports Cochran-Mantel-Haenszel odds ratios. The primary-analysis odds ratio is 3.0, with a 95% confidence interval of 1.6 to 5.4 and p < 0.001. At final analysis, the reported odds ratio is 3.1, with a 95% confidence interval of 1.7 to 5.4 and p < 0.001. Simple unadjusted calculations from posted summary counts can differ because they do not necessarily use the same adjustment or analysis method. These should not be substituted for the sponsor’s reported results.

The registry record does not flag a discrepancy between sponsor and recalculated results. Where the registry reports a sponsor analysis, it remains the primary account of that analysis. Any simple unadjusted recalculation is best treated as a transparent, descriptive check rather than as a replacement for the sponsor’s method. The record does not provide all details needed to reproduce the adjusted analyses independently.

16. Multiplicity, Missing Data and Analysis Populations

The registry record lists 18 outcome measures and 12 analyses, including several secondary outcomes and outcomes evaluated at primary and final analyses. Considering multiple endpoints and analysis times creates a multiplicity issue: the more hypotheses examined, the greater the chance that at least one result appears statistically notable by chance if no adjustment or prespecified testing hierarchy is used. The registry record does not report whether the trial used a multiplicity adjustment, a hierarchical testing procedure, or another strategy to control the overall error rate. It also does not provide enough detail to determine which secondary findings, if any, were intended to be confirmatory.

The record reports the primary analysis and several secondary findings, but the statistical analysis plan is not reported in sufficient detail to establish all prespecified decisions. Interim analyses and their potential role in the design are not reported in the registry record. The original sample-size justification is also not reported; the planning illustrations based on observed effects do not fill that gap.

The primary endpoint population is described as randomized participants with PIK3CA-mutant tumors, regardless of whether they received any amount of study treatment. That definition is useful, but the registry record does not report full analysis-population rules for every secondary endpoint. It does not state in detail how missing tumor assessments, incomplete follow-up, treatment discontinuation, or other missing observations were handled. Nor does it give a detailed accounting of the reasons participants might be absent from an endpoint analysis.

These omissions do not invalidate the posted estimates, but they limit independent evaluation of how the results were selected and analyzed. In particular, secondary p-values should be interpreted cautiously without a reported multiplicity strategy, and estimates should be understood in light of the reported endpoint-specific populations and incomplete information about missing data procedures.

17. 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: diarrhoea (8.9%), colitis (3.8%), pneumonia (2.4%), pneumonitis (2.4%), dehydration (1.7%).

The registry reports serious adverse event counts among participants at risk in the safety groups. In the placebo plus fulvestrant group, 23 of 213 participants at risk had a serious adverse event; in the taselisib plus fulvestrant group, 154 of 416 participants at risk had a serious adverse event. The registry also reports other adverse events affecting 183 of 213 and 396 of 416 participants, respectively. These are counts within the reported safety populations, which differ from the primary endpoint analysis counts.

Among the listed serious adverse event terms, diarrhoea is reported at 8.9%, colitis at 3.8%, pneumonia and pneumonitis at 2.4% each, and dehydration and hyperglycaemia at 1.7% each. The record also reports deaths of 100 participants in the placebo group and 197 in the taselisib group. A death count in a trial record should not automatically be interpreted as a treatment-related death count; the registry figures do not establish causation.

These safety summaries describe reported events, not an adjusted comparison of risk. Differences in group size, follow-up, exposure, and event ascertainment can affect raw counts, and detailed exposure-adjusted analyses are not reported in the registry record. The figures should be read alongside the endpoint results and the limits of the available safety reporting.

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

The primary result describes a statistically significant difference in investigator-assessed progression-free survival in the defined PIK3CA-mutant analysis population. The sponsor reported a hazard ratio of 0.70, with a 95% confidence interval of 0.56 to 0.89 and p = 0.004, and the median estimates were 5.39 months for placebo plus fulvestrant and 7.43 months for taselisib plus fulvestrant. These findings characterize the trial’s comparison at the posted primary analysis; they do not predict an individual participant’s outcome.

The result does not establish that every participant experienced delayed progression, nor does a group median describe the time experienced by each participant. The hazard ratio summarizes relative event rates over follow-up under the reported analysis; it is not a direct measure of an individual’s probability of progression or a difference in expected lifespan. Progression-free survival also combines progression and death, so it should not be treated as interchangeable with overall survival.

The overall-survival result at primary analysis is less conclusive: the reported hazard ratio was 0.85, with a 95% confidence interval of 0.58 to 1.25 and p = 0.415. The registry record therefore does not establish a statistically clear overall-survival difference at that time. The response outcomes are secondary and should be interpreted in view of multiple reported outcomes and the absence of a reported multiplicity strategy.

The trial was terminated, but the registry record does not report the reason. It does not report detailed procedures for missing data, interim analyses, or the original sample-size justification. Safety counts are also descriptive and do not, on their own, establish whether an event was caused by a study treatment. Taken together, the posted findings support a reading of the reported endpoint estimates and their uncertainty, not a broad claim about all outcomes, all populations, or treatment effects beyond the trial’s defined comparison.

19. Why This Trial Matters Statistically

This trial illustrates why endpoint choice matters in clinical research. Progression-free survival captures the timing of progression or death, whereas objective response records whether a specified tumor response occurred, and overall survival focuses on death from any cause. Those outcomes answer related but distinct questions. Their estimates can point in different directions or differ in precision without contradiction.

It also shows why the comparison method must match the endpoint. Medians describe the estimated event-time distribution at a particular point, while the reported hazard ratio and log-rank test use information about event timing across follow-up. For binary response, the sponsor used Cochran-Mantel-Haenszel odds ratios, while unadjusted comparisons from summary counts answer a more limited question. Treating these statistics as interchangeable would obscure what each analysis estimates.

The registry record also demonstrates the importance of reporting completeness. The primary result includes a defined population, endpoint criteria, confidence intervals, and a reported p-value, while other details—such as multiplicity control, missing-data procedures, interim analyses, and the original design justification—are not reported. That distinction helps readers separate what can be concluded from posted results from what remains uncertain about the analytic process.

Finally, statistical significance and precision are different from clinical importance. The primary confidence interval indicates a range of plausible relative effects under the analysis, but it does not by itself establish how meaningful those effects are to patients. Secondary endpoints and safety findings broaden the evidence, yet their interpretation depends on their design, analysis, follow-up, and reporting. Reading each statistic in its proper role is essential to a balanced account of a complex trial.

20. 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 analysis concerns randomized participants with PIK3CA-mutant tumors, not necessarily every participant enrolled. Although the registry describes that population, it does not provide a full endpoint-by-endpoint accounting of exclusions or missing observations. The results should therefore not be assumed to describe all enrolled participants equally.

Progression was assessed by investigators using RECIST v1.1. The registry provides the progression criteria but does not report detailed information about assessment schedules, central review, or how assessments that could not be completed were handled. The record also does not describe censoring rules or missing-data procedures in enough detail to reproduce the time-to-event analysis independently.

The study is recorded as terminated, but the reason for termination is not reported in the registry record. The original sample-size justification, interim analysis plan, and full statistical analysis plan are also not reported. The planning illustrations based on observed effects are not evidence of the sponsor’s original design decisions.

Multiple secondary outcomes and analyses are listed, but the record does not report a multiplicity-control strategy. Secondary p-values consequently have less interpretive weight than a prespecified primary test with a documented testing plan. The available overall-survival result is from the primary analysis; the registry lists a final overall-survival outcome but does not report a corresponding final estimate in these results.

Finally, adverse event counts are not adjusted for treatment exposure or follow-up in the information reported. The counts alone do not show event causality or provide a complete comparative safety analysis. These reporting limits narrow what can be concluded from the posted results without negating the estimates that are reported.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study of Taselisib + Fulvestrant Versus Placebo + Fulvestrant in Participants With Advanced or Metastatic Breast Cancer Who Have Disease Recurrence or Progression During or After Aromatase Inhibitor Therapy — NCT02340221.
• Registry record last updated 2022-07-12; status last verified 2022-07.
• Results first posted 2019-01-25.
• 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.

24. Record Summary

NCT02340221 is a randomized, double-blind, phase III, parallel-group study of taselisib plus fulvestrant versus placebo plus fulvestrant in advanced or metastatic breast cancer after recurrence or progression during or after aromatase inhibitor therapy. Overall enrollment was 631, and the registry lists the study status as terminated. Enrollment was enriched for participants with PIK3CA-mutant tumors, and the primary endpoint population was randomized participants with PIK3CA-mutant tumors, regardless of treatment received.

The primary endpoint was investigator-assessed progression-free survival under RECIST v1.1. The sponsor reported median estimates of 5.39 months and 7.43 months, a hazard ratio of 0.70, a 95% confidence interval of 0.56 to 0.89, and p = 0.004. Overall survival at primary analysis had a reported hazard ratio of 0.85, with a 95% confidence interval of 0.58 to 1.25 and p = 0.415. The record lists secondary response outcomes and safety counts, but does not report a multiplicity strategy, detailed missing-data procedures, interim analyses, or the reason for termination.