Study to Evaluate the Safety and Efficacy of NKTR-102 in Patients With Metastatic or Locally Advanced Breast Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate the Safety and Efficacy of NKTR-102 in Patients With Metastatic or Locally Advanced Breast Cancer (NCT00802945), a randomized phase 2 study. The primary outcome is Objective Response Rate (ORR).

2. Clinical Question

The study also set out to assess safety and efficacy. Its listed secondary outcomes include Kaplan-Meier estimates of progression-free survival and overall survival, survival at specified follow-up times, and treatment-emergent adverse events of NCI-CTCAE Grade 3 or higher meeting the registry’s incidence criterion. The available posted information should be read outcome by outcome: an estimate for response addresses a different clinical question from a survival estimate or an adverse-event count.

Because treatment schedule was randomized, the design was intended to compare the schedules within the enrolled trial population. The open-label design means treatment assignment was not masked. The registry record does not report further details about response assessment procedures, analysis populations, or the handling of missing assessments, so those features cannot be used to qualify the comparison.

3. Trial Design

This was a multicenter, randomized, open-label, parallel-arm Phase 2 study. The registry describes it as a two-arm, two-stage study. Enrollment is listed as 70. The study was marked completed; the recorded start is 2008-10 and primary completion is 2011-10. The registry record does not report the operational details of the stages or the reason for selecting the planned enrollment.

Eligible patients were described as having metastatic or locally advanced breast cancer whose disease had failed prior taxane-based treatment in the metastatic setting. Participants were randomized 1:1 to NKTR-102 on a q14d or q21d schedule. Both arms were assigned NKTR-102 at 145 mg/m2. The registry arm labels are NKTR-102 14 Day and NKTR-102 21 Days. There was no masking, and the parallel design means the schedules were assigned to separate groups rather than tested sequentially within the same participant.

The primary endpoint was Objective Response Rate (ORR), expressed as a percentage of subjects, with a stated timeframe of up to 2 years. The registry describes response according to RECIST v1.0 for target lesions assessed by MRI. The endpoint definition combines complete response and partial response. Secondary outcomes listed in the record include Kaplan-Meier estimates of progression-free survival, overall survival, 6-month survival, and 1-year survival, as well as treatment-emergent adverse events meeting a stated severity and incidence criterion.

The design information does not specify the randomization method, concealment procedures, the statistical analysis plan, or the original sample-size assumptions. These items are not reported in the registry record. The posted enrollment and results therefore describe the trial record but do not supply those missing design details.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

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.

6. Primary Endpoint

The registry lists the primary outcome as Objective Response Rate (ORR), measured over Up to 2 years..

Objective Response Rate is the proportion of participants classified as having either a complete response or a partial response under the registry’s stated criteria. A complete response is defined as disappearance of all target lesions. A partial response is defined as at least a 30% decrease in the sum of the longest diameter of target lesions. Assessments were described as using RECIST v1.0 for target lesions assessed by MRI. The stated timeframe is up to 2 years.

Response rate is a binary endpoint at the participant level: each participant is classified according to whether the response definition is met. Reporting it as a percentage makes the observed frequency of response in each schedule group interpretable, while the confidence interval communicates uncertainty around that estimate. It does not describe how long a response lasted, whether disease later progressed, or overall survival. Those are separate outcomes and require their own analyses.

For the 14-day arm, the posted response estimate is 28.6%, with a 95% confidence interval from 14.6% to 46.3%. For the 21-day arm, the posted estimate is 35.0%, with a 95% confidence interval from 14.6% to 46.3%. The registry also gives an unadjusted risk-difference comparison. Such a comparison expresses the difference in response proportions on the risk-difference scale; it is not an adjusted estimate and does not account for factors beyond the posted group summaries.

Response is useful as an endpoint because it gives a defined measure of tumor change under stated assessment criteria. Its interpretation remains limited to the endpoint definition and assessment period. It should not be treated as a substitute for survival, quality of life, or safety outcomes, which are not captured by the response proportion itself.

7. Results Posted in the Registry

• NKTR-102 21 Days: 34.3% (12/35) versus 28.6% (10/35) on control; risk difference 5.7 percentage points (95% CI -16.0 to 27.4), risk ratio 1.20 (0.60–2.41); unadjusted two-proportion z-test p = 0.607.

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.

Kaplan Meier Estimate of 6-month Survival

• 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:
  • NKTR-102 21 Days: 82.9% (29/35) versus 57.1% (20/35) on control; risk difference 25.7 percentage points (95% CI 5.1 to 46.3), risk ratio 1.45 (1.05–2.00); unadjusted two-proportion z-test p = 0.019.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for NKTR-102 21 Days than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Kaplan Meier Estimate of 1-year Survival

• 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:
  • NKTR-102 21 Days: 51.4% (18/35) versus 42.9% (15/35) on control; risk difference 8.6 percentage points (95% CI -14.7 to 31.9), risk ratio 1.20 (0.73–1.98); unadjusted two-proportion z-test p = 0.473.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NKTR-102 21 Days and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes broaden the questions beyond tumor response. The registry lists progression-free survival and overall survival, survival estimates at 6 months and 1 year, and treatment-emergent adverse events meeting a stated severity and incidence criterion. The posted survival estimates show a more separated schedule comparison at the earlier follow-up point than at the later point. This pattern is not a single consistent signal across all outcomes, and it does not alter what the primary response endpoint measures.

The survival outcomes are related to, but not interchangeable with, objective response. A participant may have a measured response without that response establishing a particular survival duration; conversely, survival estimates reflect time-to-event follow-up and censoring rather than the response classification alone. Progression-free survival, overall survival, and safety each address different aspects of the study. The registry record does not report numerical results for all listed secondary outcomes, so those outcomes cannot be used to fill gaps in the primary result.

Secondary findings generally carry less weight when they are unadjusted and when the analysis plan does not explain which comparisons were confirmatory. Testing multiple outcomes can yield apparently notable findings by chance, particularly when results are selected after looking across outcomes or time points. The record does not report a multiplicity strategy, hierarchy of secondary endpoints, or complete set of reported analyses. Accordingly, secondary results are best considered supportive and descriptive rather than independent confirmation of a schedule effect.

The secondary estimates also have uncertainty, and the survival methods depend on follow-up and censoring. The record does not give detailed risk sets or missing-data information. A difference at one follow-up point should therefore be considered in the context of its confidence interval, the other outcomes, the design, and the absence of a reported multiplicity plan. It should not be treated as proof of an overall pattern or as evidence that the schedules differ on every clinically relevant outcome.

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

• Kaplan Meier Estimate of Progression-Free Survival (PFS)
• Kaplan Meier Estimate of Overall Survival (OS)
• Kaplan Meier Estimate of 6-month Survival
• Kaplan Meier Estimate of 1-year Survival
• Percent of Patients With Treatment-Emergent Adverse Events (TEAE): NCI-CTCAE Grade 3 or Higher With Incidence Rate ≥ 2% in Either Treatment Group

9. Statistical Interpretation

10. Statistical Methods Explained

The registry presents the primary outcome as a percentage of participants with a response and gives a 95% confidence interval for each arm. It also presents an unadjusted comparison between schedules. These are descriptive and inferential summaries of the posted results. The registry record does not report the original statistical analysis plan, so the precise planned tests, any adjustment strategy, and the prespecified handling of analysis populations are not reported in the registry record.

What does a risk difference describe?

A risk difference subtracts one group’s event proportion from the other group’s event proportion, retaining the original proportion scale. For the primary endpoint, the posted estimate is 0.057. Its 95% confidence interval extends from -0.160 to 0.274. A positive estimate indicates a larger observed proportion in the 21-day arm relative to the 14-day arm under the comparison’s stated direction; a negative value would indicate the reverse. An interval spanning both positive and negative values indicates that the data do not pin down the direction with precision.

This measure differs from a risk ratio or an odds ratio. A risk ratio compares proportions as a ratio, while an odds ratio compares odds. These measures can communicate relative contrasts, but their numerical scale and interpretation differ from a risk difference. The registry contains recalculated relative measures, but the primary interpretation centers on the absolute risk-difference scale. Since the discrepancy flag is false, there is no indicated conflict with the sponsor’s own analysis; in cases of a discrepancy, the sponsor’s own analysis takes precedence.

How should the p-value be read?

The primary comparison has an unadjusted p-value of 0.607. In general, a p-value measures how unusual data at least as incompatible with a specified null model would be, assuming that model and the test assumptions. It is not the probability that a treatment effect is absent, and it does not measure the probability that the observed difference is due to chance. It should be read alongside the effect estimate and its confidence interval, not as a stand-alone verdict.

The p-value is described as unadjusted. That matters because the registry lists more than one outcome, and no multiplicity adjustment is reported. A collection of unadjusted tests does not have the same error properties as a single prespecified test. The registry record does not state whether the primary comparison was the only confirmatory test or how secondary comparisons were intended to be interpreted.

What does a confidence interval contribute?

A confidence interval gives a range of estimates compatible with the observed data under the interval method’s assumptions. In repeated use of the same method, intervals constructed this way would have the stated coverage property. It is not a range that assigns a probability to the fixed, true effect after the data have been observed. A wide interval signals limited precision; an interval including no difference does not establish that there is no effect. Clinical importance also depends on the plausible effect sizes, not only on whether an interval includes zero.

For the primary arm estimates, the reported intervals are 14.6% to 46.3% for both groups. For the risk difference, the interval is -0.160 to 0.274. The endpoints of a group-specific interval and a difference interval answer different questions, and their overlap is not a formal test of the between-group contrast. The direct comparison interval is the relevant uncertainty summary for the risk difference.

Why are survival estimates different from response proportions?

Objective response is summarized as a participant-level percentage meeting the response definition. Kaplan-Meier estimates instead use time-to-event information. They estimate the probability of remaining free of the specified event over follow-up while accounting for participants whose event status becomes unknown after their last observation, under censoring assumptions. Such participants are censored rather than automatically counted as events or as event-free for all later time.

That distinction is relevant to the secondary survival outcomes. The registry provides estimates at 6 months and 1 year and gives confidence intervals and unadjusted comparisons. It does not report the numbers at risk over time, censoring details, or the detailed time-to-event analysis outputs. The registry record also does not report the time-to-event analysis populations or a proportional-hazards assessment. Consequently, these estimates can be described as posted Kaplan-Meier results, but their underlying assumptions and robustness cannot be fully assessed from the record.

What does randomization support?

Random allocation is intended to make treatment groups comparable on average with respect to both measured and unmeasured factors. It supports a comparative interpretation, but does not remove uncertainty in a study of this size or ensure that every prognostic feature is balanced in the realized groups. Open-label assignment means participants and study personnel knew the assigned schedule, which can influence care, reporting, or assessment depending on the outcome. The registry record does not report masking of outcome assessors or procedures to limit assessment bias.

The posted numerical comparison is unadjusted. The record does not state whether an adjusted analysis was planned, whether all randomized participants were included in each endpoint analysis, or how missing data were handled. These omissions are relevant to the interpretation of both response and survival estimates. The estimates should therefore be read as the results reported in the registry, not as a complete reconstruction of the trial’s statistical analysis.

11. Confidence Intervals and Precision

Precision is reflected in the range of values compatible with the data under the confidence-interval method. For the primary response endpoint, both arm-specific 95% confidence intervals extend from 14.6% to 46.3%. The posted risk-difference estimate is 0.057, with a 95% confidence interval from -0.160 to 0.274. The comparison interval is broad and includes both a negative and a positive difference, so the observed point estimate should not be treated as a precise estimate of the schedule contrast.

The arm-specific estimates and the direct contrast answer distinct questions. The former estimate response within each schedule group; the latter estimates how those response proportions differ. Their uncertainty should be read from their respective intervals. In general, confidence intervals express sampling uncertainty under the method’s assumptions. They do not cover every source of uncertainty, such as measurement differences, missing data, or limitations in the analysis plan.

The secondary survival intervals also show varying precision. At 6 months, the posted risk-difference confidence interval is 0.051 to 0.463. At 1 year, it is -0.147 to 0.319. These intervals describe uncertainty in the corresponding comparisons; the 6-month result is not a substitute for the primary endpoint, and the 1-year interval includes values on either side of no difference. Because the estimates are based on Kaplan-Meier methods, their precision depends in part on event and censoring information that is not detailed in the registry record.

Confidence intervals should not be interpreted as proving equivalence when they include zero, nor as proving meaningful benefit when they do not. The record does not specify a clinically important difference for response or survival. Without such a threshold, statistical uncertainty can be described, but whether the range represents an important clinical difference cannot be resolved from the posted results alone.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design assumptions. The registry record does not report the assumptions used to choose the study’s planned enrollment. For the primary binary response comparison, the planning figures are participants per arm. For time-to-event tables, the figures are total events using the Schoenfeld method; the other tables give participants per arm.

The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They consider effects equal to the observed effect and fractions of that observed effect. The rows labelled for a fraction of the observed effect should be read as hypothetical planning scenarios: they ask how much enrollment would be needed if a future study aimed to detect a smaller effect than the one observed. Smaller effects generally require more participants to distinguish them from random variation with a chosen degree of power.

The 80% power column describes a planning target: under the stated assumptions and a specified true effect, the design would have an 80% chance of detecting that effect using the stated test criterion. The 90% power column describes the corresponding target at 90%. Higher planned power usually requires more participants or events, all else held constant. The table’s values are not a recommendation and do not account for unreported design features, attrition, or other analysis choices.

These calculations use the observed effect as their starting point, so they can be unstable when that estimate is uncertain. They should be treated as planning illustrations rather than proof that the current trial had adequate or inadequate power. This is not observed power. The sample-size assumptions used in the trial’s original design are not reported in the registry record.

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 = 0.286; treatment proportion p₁ = 0.343; average p̄ = 0.314.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6565 = 1.2868.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6553 = 0.5515.
4. n = (1.2868 + 0.5515)² / (0.0571)² = 1,034.9, rounded up to 1,035 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 <- 0.285714285714286                          # control proportion
p1 <- 0.342857142857143                          # 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(802945)
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 = 1,035 (80% power), 1,385 (90% power)
 75% of observed effect: n per arm = 1,818 (80% power), 2,433 (90% power)
 50% of observed effect: n per arm = 4,038 (80% power), 5,404 (90% power)
power.prop.test: 1034.9 
Simulated power at n = 1,035 per arm: 0.800 (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

The registry lists a primary endpoint and several secondary outcomes, but the statistical plan is not reported in the registry record. In particular, it does not report whether testing was organized in a hierarchy, whether any multiplicity adjustment was planned, or which secondary comparisons were intended to be confirmatory. Without this information, the unadjusted p-values should not be interpreted as if they accounted for all outcome comparisons.

Multiplicity is the general problem that testing many hypotheses can increase the chance of obtaining one or more apparently positive results even when the underlying effects are absent. Different approaches can control that risk, but no specific approach can be attributed to this trial based on the registry record. The secondary findings should therefore be read with caution and in conjunction with their estimates and confidence intervals, rather than ranked only by p-value.

Missing-data handling is also not reported in the registry record. The record does not specify how participants without a response assessment were classified, whether any imputation was used, or how deviations from assigned schedules were handled. For time-to-event outcomes, it does not provide censoring details, numbers at risk, or information on how incomplete follow-up was addressed. Those details matter because the assumptions behind the analysis can affect the estimates.

The analysis populations are not reported in the registry record. It is not clear from the posted information whether the response analysis included all randomized participants, only those who received treatment, or another defined group. The same issue applies to the secondary endpoints. Randomization supports a comparison based on assigned groups when analyzed appropriately, but a reader cannot verify the exact population strategy from the registry information alone.

The record also does not report interim analyses or stopping rules. It describes a two-stage study, but the stages’ statistical purpose and any decision criteria are not reported in the registry record. These missing details limit assessment of how the final comparisons relate to the original plan.

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 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 (17.1%), disease progression (11.4%), dehydration (11.4%), fatigue (5.7%), dizziness (5.7%).

The registry safety figures list serious adverse events affecting 18 participants in the NKTR-102 14 Day group and 15 in the NKTR-102 21 Days group; 35 participants are listed at risk in each group. The record also lists deaths as 27 and 23, respectively. These are descriptive counts in the registry and do not establish that the drug or schedule caused an event or death. The record does not provide a causal attribution analysis or enough detail to interpret the death counts as a treatment effect.

The most frequently listed serious adverse-event terms are Diarrhoea (17.1%), Disease Progression (11.4%), Dehydration (11.4%), Fatigue (5.7%), Dizziness (5.7%), and Nausea (5.7%). The listed terms are not broken out by schedule in the posted serious-event term information, so they should not be assigned to a particular arm. Serious-event counts are distinct from the listed secondary outcome concerning treatment-emergent adverse events of NCI-CTCAE Grade 3 or higher; the record does not provide a full arm-specific result for that secondary outcome in the registry record.

Safety counts depend on definitions, follow-up, ascertainment, and attribution. Those details are not fully reported in the registry record. The counts can describe what was recorded, but do not alone establish comparative safety or rule out events that were not captured.

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

The posted primary endpoint estimates describe objective responses under the registry’s RECIST v1.0 definition. The response estimate is 28.6% for the 14-day schedule and 35.0% for the 21-day schedule. The unadjusted risk-difference estimate is 0.057, and its 95% confidence interval, from -0.160 to 0.274, reflects substantial uncertainty about the size and direction of the schedule contrast. The unadjusted p-value is 0.607.

These results do not establish that the schedules are equivalent, because an equivalence margin and a corresponding analysis are not reported. They also do not establish superiority of either schedule. A non-significant p-value is not proof of no difference, while a difference between point estimates is not by itself proof of a reliable or clinically important effect. The confidence interval includes a range of plausible differences in either direction.

The secondary survival estimates address separate outcomes and have their own uncertainty. They should not be used to reinterpret the primary response result as though all outcomes measured the same effect. In addition, the registry does not report a multiplicity plan, analysis populations, or complete missing-data procedures. These omissions make it difficult to judge how much weight to place on individual unadjusted secondary findings.

The results apply to the population and setting described in this Phase 2 trial: patients with metastatic or locally advanced breast cancer whose disease had failed prior taxane-based treatment in the metastatic setting. The record does not report enough information to establish how well the findings apply to other populations, treatment settings, or schedules. The open-label design and the absence of detailed assessment procedures also leave uncertainty about potential measurement or performance effects.

Finally, efficacy and safety should be considered separately. Response percentages do not establish survival benefit or safety, and adverse-event counts do not establish causation. The registry figures describe trial outcomes; they are not a basis for individual treatment decisions.

17. Why This Trial Matters Statistically

This trial is statistically informative as a randomized comparison of two schedules of the same drug, with the same stated dose in both arms. That design focuses the comparison on schedule rather than on different drugs or a drug versus no treatment. The primary endpoint is a clearly defined response proportion, and the record supplies arm estimates, confidence intervals, and an unadjusted comparative estimate.

The main statistical lesson is the distinction between an observed point estimate and its precision. The response percentage is numerically higher in the 21-day arm, but the risk-difference interval is wide and extends in both directions around no difference. The p-value alone cannot establish equivalence or clinical importance. A reader needs the estimate, interval, endpoint definition, and design together to understand what the trial can and cannot say.

The study also illustrates why secondary outcomes require context. Survival estimates can inform questions that response rate does not answer, but they are analyzed differently and rely on follow-up and censoring assumptions. When several outcomes are reported without a stated multiplicity strategy, isolated unadjusted findings should be treated cautiously. A secondary pattern is not automatically confirmation of the primary result.

Finally, registry reporting determines how fully a result can be assessed. Details about analysis populations, missing data, interim analyses, and the original statistical plan are not reported in the registry record. Their absence does not invalidate the posted estimates, but it limits independent assessment of the analysis choices and the robustness of the conclusions. The trial therefore provides a useful example of reading estimates and uncertainty without overstating what a Phase 2 comparison can establish.

18. Limitations

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

Several trial-specific limitations affect interpretation. The study is open-label, so treatment assignment was not masked. The registry record does not say whether response assessors were masked or describe procedures to reduce assessment bias. Because the primary endpoint depends on lesion assessment, the absence of those details limits evaluation of possible measurement effects.

The registry describes a two-stage study but does not report the purpose of the stages, stage-specific decision rules, or whether interim analyses occurred. The original sample-size justification and statistical assumptions are also not reported in the registry record. The planning illustrations based on the observed effect are not a substitute for the original design rationale.

Analysis populations, missing-data procedures, and the handling of participants who did not complete assessments are not reported. For survival outcomes, the record does not supply the detailed risk sets, censoring pattern, or time-to-event analysis outputs needed to assess the estimates fully. The record also does not report a multiplicity plan for the several listed endpoints.

The posted comparison is unadjusted, and no adjusted analysis is reported in the registry record. The enrollment and results concern the trial’s stated population and should not automatically be generalized to other groups or settings. Finally, the safety information is limited to the reported counts and event terms; detailed attribution, timing, and full arm-specific results for all listed safety outcomes are not reported. These limits do not change the numerical results, but they constrain how confidently those results can be interpreted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study to Evaluate the Safety and Efficacy of NKTR-102 in Patients With Metastatic or Locally Advanced Breast Cancer — NCT00802945.
• Registry record last updated 2018-07-09; status last verified 2018-06.
• Results first posted 2018-07-09.
• 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

NCT00802945 is a completed, multicenter, randomized, open-label, parallel-arm Phase 2 study of NKTR-102 in patients with metastatic or locally advanced breast cancer whose disease had failed prior taxane-based treatment in the metastatic setting. The registry lists enrollment as 70 and describes a two-stage study. The recorded start is 2008-10, and primary completion is 2011-10.

Participants were randomized 1:1 to NKTR-102 at 145 mg/m2 on a q14d or q21d schedule. The primary outcome was Objective Response Rate, defined using RECIST v1.0 criteria for target lesions assessed by MRI. The posted response estimates were 28.6% and 35.0%, respectively; the unadjusted risk-difference estimate was 0.057 with a 95% confidence interval from -0.160 to 0.274 and an unadjusted p-value of 0.607.

Secondary outcomes include survival and safety measures. The registry record does not report the original statistical plan, multiplicity strategy, analysis populations, or missing-data procedures. Those omissions limit assessment of the full analysis and its assumptions.