Efficacy and Safety of Pazopanib Monotherapy After First Line Chemotherapy in Ovarian, Fallopian Tube, or Primary Peritoneal Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Pazopanib Monotherapy After First Line Chemotherapy in Ovarian, Fallopian Tube, or Primary Peritoneal Cancer (NCT00866697), a randomized phase 3 study. The primary outcome is Investigator-assessed Progression-free Survival (PFS).

2. Clinical Question

3. Trial Design

This was a randomized, double-masked, phase III study of pazopanib monotherapy versus placebo. It enrolled 940 participants and is recorded as completed. The study concerned women with epithelial ovarian, fallopian tube, or primary peritoneal cancer whose cancer had not progressed on first-line chemotherapy. The registry lists Novartis Pharmaceuticals as sponsor. The recorded start date is 2009-05-26, and the primary completion date is 2012-07-08.

The pazopanib group received an oral 800 mg tablet once daily for up to 24 months. The placebo group received a matched tablet orally once daily for up to 24 months. Random allocation supports a comparison between the assigned groups by reducing the influence of systematic differences at baseline, while masking can limit some forms of expectation-related influence. Those are general design purposes; the registry record does not describe the randomization sequence, allocation concealment, or masking procedures in further detail.

The primary endpoint was investigator-assessed progression-free survival in the Intent-to-Treat population, described as all randomized participants. The time origin was randomization, and the event was disease progression or death due to any cause. The registry reports median follow-up of 17.9 months for pazopanib and 12.3 months for placebo for this endpoint. These follow-up summaries are not the same as the median progression-free survival estimates.

The record lists 20 outcome measures and 18 posted secondary outcomes. Secondary topics include overall survival, progression-free survival using Gynecologic Cancer Intergroup criteria, three-year progression-free survival, and changes in quality-of-life and symptom scores. The registry record does not report the original sample-size justification, the trial’s planned statistical analysis details beyond the reported log-rank analyses, or whether interim analyses were planned or conducted.

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:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat (ITT) Population: all randomized participants

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 Investigator-assessed Progression-free Survival (PFS), measured over From the date of randomization until the date of progression or death due to any cause (median time of follow-up was 17.9 months for pazopanib and 12.3 months for placebo).

Investigator-assessed progression-free survival measures the interval from randomization until the first qualifying event: disease progression or death due to any cause. Progression was defined using Response Evaluation Criteria in Solid Tumors (RECIST). The registry description specifies progression based on changes in target lesions or the appearance of new lesions, as well as progression of non-target lesions. Participants without recorded progression or death were censored at their last adequate assessment under the stated rules.

This is a time-to-event endpoint. It accounts for both whether an event occurred and when it occurred, rather than treating every participant’s follow-up as if it lasted the same length of time. The median is the time by which half of the estimated event-time distribution has experienced the event, under the analysis method. It is a summary of the distribution, not an average individual’s experience and not a statement that every participant had that duration.

Progression-free survival is used in trials because it captures progression as well as death and can therefore describe disease control before death occurs. General methodological considerations include how progression is assessed, how often assessments occur, and how censoring is handled. The registry reports specific censoring rules, including censoring at the last adequate assessment for participants who started a new anti-cancer therapy before documented progression or death, and for certain events after an extended gap without adequate assessment. Whether assessments were centrally reviewed or how disagreements were resolved is not reported in the registry record.

7. Results Posted in the Registry

• Placebo vs Pazopanib 800 mg: hazard ratio 0.77 (95% CI 0.64–0.91), reported p = 0.002 (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.

Overall Survival - Median

• 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 vs Pazopanib 800 mg: hazard ratio 0.96 (95% CI 0.81–1.15), reported p = 0.643 (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 vs Pazopanib 800 mg and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a range of secondary topics, including overall survival, other progression-free survival summaries, and quality-of-life or symptom measures. The posted overall-survival analysis reports a hazard ratio of 0.960, with a 95% confidence interval from 0.805 to 1.145 and p = 0.643. That result does not provide clear statistical evidence of a difference in overall survival in the reported analysis. It should not be treated as evidence that the groups are equivalent.

The registry record lists 18 posted secondary outcomes, but does not provide numerical results for every secondary measure in the record. Specific secondary endpoint values beyond the reported overall-survival results are not reported in the registry record. Therefore a broad claim that the secondary outcomes consistently support, contradict, or replicate the primary result cannot be made from the available outcome details.

Secondary endpoints address related but distinct questions. Overall survival concerns time to death, while quality-of-life and symptom measures concern participant-reported or functional dimensions; these outcomes need not move in the same way or on the same time scale as progression-free survival. General interpretation should consider each endpoint’s definition, measurement timing, missingness, and analysis population rather than assuming that one endpoint stands in for another.

Multiple secondary comparisons create a multiplicity concern: when many hypotheses are tested, some apparently notable findings can occur by chance even if there is no underlying effect. Unadjusted secondary results therefore generally carry less confirmatory weight than a prespecified primary result, unless a suitable hierarchy or multiplicity procedure was planned and applied. Whether adjustment was used for this trial is not reported in the registry record. Secondary findings are best treated as supportive or exploratory unless the analysis plan establishes stronger confirmatory status.

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

• Overall Survival - Median
• Overall Survival: Number of Participants Experiencing Death
• Progression-free Survival Per Gynecologic Cancer Intergroup (GCIG) Criteria
• 3-year Progression-free Survival
• Change From Baseline in the European Organization for the Research and Treatment of Cancer (EORTC) QLQ-C30 Global Health Status Score on Day 1 of Week 13 and Months 7, 10, 13, 16, and 25
• Change From Baseline in QLQ-OV-28 Module Attitude to Disease/Treatment Functional Score on Day 1 of Week 13 and Months 7, 10, 13, 16, and 25
• Change From Baseline in QLQ-OV-28 Module Body Image Functional Score on Day 1 of Week 13 and Months 7, 10, 13, 16, and 25
• Change From Baseline in QLQ-OV-28 Module Peripheral Neuropathy (PN) Symptoms Score at Week 13 and Months 7, 10, 13, 16, and 25

9. Statistical Interpretation

10. Statistical Methods Explained

The analyses described for the primary and overall-survival outcomes are time-to-event analyses. This approach is used when the outcome is the time until an event and participants may have different amounts of follow-up. The primary event was progression or death due to any cause; the overall-survival event was death due to any cause.

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

A median time-to-event estimate marks the point at which the estimated event-time distribution reaches its midpoint. It summarizes the group’s event-time experience but does not tell how long each participant lived without the event. It also does not use the same information as a simple mean: participants who have not experienced an event by their last assessment can still contribute follow-up time without being assigned an event time.

For the primary endpoint, the posted medians were 17.9 months for pazopanib and 12.3 months for placebo. For overall survival, they were 59.1 months and 64.0 months, respectively. Those estimates are descriptive summaries of their respective time-to-event distributions. They should not be treated as direct substitutes for the hazard ratio, which uses event information across follow-up rather than comparing only the two median values.

What does censoring mean in this analysis?

Censoring occurs when a participant’s event time is not observed during the period counted by the analysis. In general, a censored participant contributes information up to the censoring time; the analysis does not treat that time as if an event had occurred. Censoring is not automatically a loss of all information, but interpretation depends on the reasons for censoring and on the assumptions used by the analysis.

The registry states that participants who did not progress or die were censored at the date of their last adequate assessment. Participants who began a new anti-cancer therapy before radiological progression or death were censored at the last adequate assessment before that therapy. It also describes censoring at the last visit with an adequate assessment before progression or death when an extended period without an adequate assessment preceded the event. These rules define how certain observations entered the analysis. The registry record does not describe the amount of censoring by group or provide a fuller analysis of the reasons for censoring.

How should the hazard ratio be read?

The reported hazard ratio is 0.766 for the primary comparison, with a 95% confidence interval from 0.643 to 0.911. A hazard ratio is a relative comparison of event rates over time under the analysis; it is not a percentage change in median progression-free survival, and it does not mean that an individual’s event risk is reduced by that amount. The direction of interpretation depends on which group is in the numerator and on the event coding. The registry labels the comparison Placebo vs Pazopanib 800 mg and reports the estimate; descriptions should retain that reported comparison rather than inventing a different orientation.

The log-rank method compares time-to-event experience between groups while accounting for censoring. In general, it tests whether the observed event patterns differ over follow-up. The reported primary p-value is 0.002. A p-value describes how compatible the observed data are with a specified null hypothesis under the method’s assumptions; it is not the probability that the null hypothesis is true, nor a measure of clinical importance. The registry record reports the log-rank method but does not supply further details about model checks or additional covariate adjustment.

Why are confidence intervals useful?

A confidence interval expresses uncertainty around an estimate under the statistical method. The primary hazard-ratio interval ranges from 0.643 to 0.911, and the overall-survival hazard-ratio interval ranges from 0.805 to 1.145. The width and position of an interval help readers assess precision and which values remain compatible with the data under the method. A 95% confidence interval does not mean there is a 95% probability that the fixed true value lies inside this particular interval; it describes the long-run behavior of the interval procedure under its assumptions.

The intervals for median times also matter. The primary medians have intervals of 15.9 to 21.8 months for pazopanib and 11.8 to 17.7 months for placebo. The overall-survival medians have intervals of 53.5 to 71.6 months for pazopanib and 56.0 to 75.7 months for placebo. Overlap between separate group-specific intervals is not itself a formal test of the treatment comparison. The reported hazard-ratio analysis addresses the comparison directly.

What is known about the analysis specification?

The primary analysis population is stated as the Intent-to-Treat population, comprising all randomized participants. This population preserves the randomized group assignment for analysis and generally supports interpretation of the randomized comparison. The registry reports the log-rank method and sponsor hazard ratio. It does not report the original protocol’s full statistical analysis plan, adjustment covariates, interim-analysis plan, or multiplicity strategy. Those details should not be assumed from the posted estimates.

General statistical practice distinguishes a prespecified primary analysis from secondary or exploratory analyses. Results across multiple endpoints can arise from chance, particularly when many tests are considered. Adjustment procedures or a hierarchy can manage some of that concern, but whether such procedures were used for this trial is not reported in the registry record. Therefore the primary result and the additional outcomes should not automatically be treated as having equal evidential weight.

11. Confidence Intervals and Precision

The primary hazard-ratio estimate is 0.766, with a 95% confidence interval from 0.643 to 0.911. The interval lies below 1 and gives a range of values compatible with the data under the reported analysis and its assumptions. Its width still leaves uncertainty about the magnitude of the comparison; the estimate should not be treated as exact. The p-value of 0.002 is consistent with evidence against the null comparison under the log-rank analysis, but it does not remove uncertainty about the effect size.

The group-specific median progression-free survival estimates also have uncertainty: 17.9 months for pazopanib, with an interval from 15.9 to 21.8 months, and 12.3 months for placebo, with an interval from 11.8 to 17.7 months. These intervals describe precision around each median, not a confidence interval for the difference between medians. The sponsor-reported hazard ratio is the direct comparative statistic posted for the primary outcome.

For overall survival, the hazard ratio is 0.960, with a 95% confidence interval from 0.805 to 1.145. This interval includes 1 and is compatible with a range of possible comparisons that includes no difference as well as values on either side. Its p-value is 0.643. The median estimates also have broad intervals: 59.1 months for pazopanib, with an interval from 53.5 to 71.6 months, and 64.0 months for placebo, with an interval from 56.0 to 75.7 months.

Confidence intervals describe statistical uncertainty, not all uncertainty. They do not capture every concern about endpoint assessment, censoring, missing observations, applicability to other populations, or unreported analysis choices. The registry record gives the stated estimates and intervals but not enough detail to assess all such sources. Precision should therefore be considered alongside the design and the limits of the recorded methods.

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 for time-to-event outcomes are counts of total events, not participants per arm. The primary-outcome illustrations include 442 total events for 80% power and 592 total events for 90% power when planning for 100% of the observed effect. When planning for 75% of the observed effect, the corresponding figures are 786 and 1,052 total events; for 50% of the observed effect, they are 1,768 and 2,366 total events.

The columns describe different planning targets. A design targeting 80% power has an 80% chance, under the specified assumptions and effect, of detecting the stated effect at the chosen significance level. The 90% power column represents a higher chance of detection under those same assumptions. Power is a property of a planned study under assumptions, not a measure of how likely the observed result is true.

The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. For time-to-event calculations, the method is Schoenfeld and the target is total events. The registry record does not report the trial’s original sample-size justification or original design assumptions; these planning illustrations are computed from the observed effect and are not a reconstruction of the original design.

Smaller target effects require more information to detect reliably, which is why the event targets increase as the planning effect moves from 100% to 75% to 50% of the observed effect. These figures are planning illustrations, not observed power. They should not be interpreted as the number of participants who were enrolled or as a statement about the probability that the completed trial’s finding is correct.

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 = 0.766, so ln(HR) = -0.2666.
2. d = 4 × (1.96 + 0.842)² / [ln(0.766)]² = 441.8, rounded up to 442 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 <- 0.766                              # 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(866697)
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 = 442 (80% power), 592 (90% power)
 75% of observed effect: events = 786 (80% power), 1,052 (90% power)
 50% of observed effect: events = 1,768 (80% power), 2,366 (90% power)
Simulated power with 442 events: 0.799 (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 769 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 940 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 <- 12.3          # control-arm median, months (converted from the posted unit)
hr          <- 0.766          # 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: 602         p (1-sided)   0.0001
 Events: 200        ~HR at bound   0.5910
   Month: 19    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.77   0.0338
   IA 2: 67%                   Z   2.5114
      N: 770         p (1-sided)   0.0060
 Events: 399        ~HR at bound   0.7774
   Month: 30    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.77   0.5603
       Final                   Z   1.9930
      N: 770         p (1-sided)   0.0231
 Events: 598        ~HR at bound   0.8495
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.77   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 posted primary comparison is the sponsor-reported log-rank analysis: hazard ratio 0.766, 95% confidence interval 0.643 to 0.911, and p = 0.002. The overall-survival analysis reports a hazard ratio of 0.960, 95% confidence interval 0.805 to 1.145, and p = 0.643. These are the reported comparative results and should be distinguished from planning illustrations based on observed effects.

No discrepancy is flagged between the posted data and the sponsor’s reported analysis. Where a discrepancy is flagged, the sponsor’s own analysis takes precedence over simple unadjusted recalculations from posted summary statistics. In this record, the interpretation rests on the sponsor-reported hazard ratios and their intervals and p-values; no competing recalculated estimate is described.

Recalculations based on summary statistics, when available, cannot reproduce every detail of a trial analysis. They may not reflect the exact participant-level event histories, censoring, stratification, or analysis specification. The registry record identifies the log-rank method but does not report all protocol and analysis-plan details. The reported sponsor analysis is therefore the appropriate primary reference for the posted comparison, while the stated limits of the record remain relevant.

16. Multiplicity, Missing Data and Analysis Populations

The registry record identifies investigator-assessed progression-free survival as the primary outcome and lists multiple secondary outcomes, including overall survival, additional progression-free survival measures, and changes in quality-of-life and symptom scores. Having several outcomes can be useful because different measures capture different aspects of the study question. It also creates a statistical issue: testing many hypotheses increases the chance of obtaining at least one apparently significant result by chance when all null hypotheses are true.

General approaches to multiplicity include adjusting significance thresholds, controlling a family-wise error rate, or specifying a hierarchical testing sequence. These approaches affect how strongly individual secondary results can be interpreted. The registry record does not report whether any multiplicity adjustment, testing hierarchy, or family of endpoints was specified for this trial. It also does not report whether interim analyses were planned or conducted. Those choices should not be inferred from the reported p-values.

The primary analysis population is stated as the Intent-to-Treat population, defined as all randomized participants. This clarifies the stated population for the primary endpoint, but the registry record does not describe the handling of missing outcome assessments in detail beyond the stated censoring rules. For progression-free survival, participants without progression or death were censored at their last adequate assessment, with additional rules for starting new anti-cancer therapy before an event and for events after an extended period without adequate assessment. The number and distribution of censored observations, and the results of sensitivity analyses, are not reported in the registry record.

For other outcomes, including quality-of-life measures, the missing-data methods and analysis populations are not reported in the registry record. Missingness can affect an estimate when the likelihood of an absent measurement is related to participants’ health or their unobserved outcome. General statistical methods can address some missing-data settings, but their validity depends on assumptions. Without the analysis plan and fuller outcome-level details, it is not possible to assess those assumptions or determine how missing values affected secondary results.

The registry provides useful definitions and summary results, but it is not a substitute for a full protocol and statistical analysis plan. The original sample-size justification, detailed analysis specifications, multiplicity strategy, interim-analysis information, and fuller missing-data procedures are not reported in the registry record.

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: alanine aminotransferase increased (3.8%), pyrexia (1.9%), hypertension (1.7%), aspartate aminotransferase increased (1.5%), hepatic enzyme increased (1.0%).

The registry reports serious adverse events among participants at risk in each group. In the placebo group, 51 participants were affected among 461 at risk; in the pazopanib group, 121 were affected among 477 at risk. The record also lists other adverse events: 381 participants among 461 at risk for placebo and 462 among 477 at risk for pazopanib. These are counts with their recorded denominators, not estimates of treatment causation.

Deaths recorded in the adverse-event summary were 0 for placebo and 3 for pazopanib. The registry lists the most frequent serious adverse-event terms with percentages, including Alanine aminotransferase increased at 3.8%, Pyrexia at 1.9%, Hypertension at 1.7%, Aspartate aminotransferase increased at 1.5%, Hepatic enzyme increased at 1.0%, and Thrombocytopenia at 0.8%. These terms and percentages are the posted summary, not a complete account of every adverse event.

Adverse-event counts describe events recorded during the study; they do not by themselves establish that the intervention caused an event. The at-risk denominators differ from the randomized group counts reported for the primary efficacy analysis. Reasons for that difference, event collection details, severity definitions, and exposure-adjusted safety analyses are not reported in the registry record. Safety interpretation should therefore remain descriptive and limited to the posted information.

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

The primary result shows a statistically detectable difference in investigator-assessed progression-free survival between the randomized groups under the sponsor-reported log-rank analysis. The reported medians were 17.9 months for pazopanib and 12.3 months for placebo, and the hazard ratio was 0.766 with a 95% confidence interval from 0.643 to 0.911. The interval and p-value describe evidence under the stated analysis; they do not guarantee that an individual participant will experience a particular outcome.

The result does not establish that every participant benefited, quantify an individual’s chance of progression, or show that the same result applies to people who differ from the trial population. It does not mean that the median times are predictions for any one person. The trial studied women with the stated cancer types whose disease had not progressed on first-line chemotherapy, and the primary analysis was defined for all randomized participants.

The overall-survival comparison is less conclusive in the posted analysis: the hazard ratio is 0.960, with a 95% confidence interval from 0.805 to 1.145 and p = 0.643. This does not demonstrate equivalence or prove there is no difference. It indicates that the analysis did not provide clear statistical evidence of an overall-survival difference. The progression-free survival and overall-survival findings concern different endpoints and should not be collapsed into a single claim.

The record’s safety summaries report serious adverse events, other adverse events, deaths, and selected serious-event terms. Those counts are descriptive and do not alone establish causation or fully characterize risk. The primary result should be read alongside the safety information, endpoint assessment rules, follow-up, and limits in the registry record.

Finally, statistical evidence is not the same as a complete assessment of clinical importance. The registry record does not supply all information needed to judge outcome-assessment procedures, multiplicity, missing-data assumptions, or the original analysis plan. The findings support interpretation of this trial’s recorded comparison, not a broader guarantee about treatment outcomes.

19. Why This Trial Matters Statistically

This trial illustrates why time-to-event results need more than a pair of medians. The primary endpoint includes both progression and death and accounts for differing follow-up through censoring. The sponsor-reported hazard ratio uses event information across follow-up, while the medians provide an accessible summary of each group’s event-time distribution. Together, these statistics describe different aspects of the same endpoint and should not be treated as interchangeable.

It also illustrates the importance of reading precision alongside statistical significance. The primary hazard-ratio interval lies below 1, while the overall-survival interval includes 1. Those intervals communicate uncertainty and are more informative than a binary significant-or-not label alone. The secondary overall-survival result also demonstrates why an endpoint that may be related to the primary outcome can produce a different estimate and degree of evidence.

The study’s randomization and masking are important design features for interpreting a comparison. At the same time, results depend on how progression was defined, how assessments were handled, and how censoring was applied. The registry describes RECIST-based progression and several censoring rules, but does not report all details of the study’s protocol or analysis plan. Transparent reporting of those details helps readers judge whether the analysis addresses the intended question.

Finally, the trial record highlights the distinction between observed trial results and planning calculations. Event targets based on the observed effect can illustrate how information needs change when a smaller effect is targeted. They do not explain the original trial’s design or constitute observed power. Keeping these concepts separate helps avoid treating an after-the-fact planning illustration as evidence about the completed study’s success or failure.

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 registry record does not report the original sample-size justification, so the planning illustrations based on the observed effect cannot establish what assumptions guided the trial’s design. The full protocol and statistical analysis plan are also not reported, including details of interim analyses, multiplicity control, and any planned hierarchy for secondary outcomes.

The primary endpoint was investigator-assessed. The registry describes RECIST-based progression but does not report whether assessment was independently reviewed, whether assessors were centrally adjudicated, or how disagreements were resolved. Although the study is described as double-masked, further details about masking procedures and which roles were masked are not reported in the registry record.

The posted progression-free survival summaries include median follow-up of 17.9 months for pazopanib and 12.3 months for placebo. The registry does not report the full follow-up distributions or provide enough information to assess why the group medians differ. It gives censoring rules but not the extent of censoring by group, detailed reasons for censoring, or sensitivity analyses addressing those rules.

The record does not provide numerical results for every listed secondary outcome. It also does not report detailed missing-data methods for quality-of-life and symptom measures or whether secondary analyses used multiplicity adjustment. As a result, the breadth and consistency of evidence across secondary outcomes cannot be fully assessed from the registry record.

The safety summary reports counts, denominators, deaths, and selected serious-event terms, but does not report all details needed for a fuller comparative safety analysis, such as exposure-adjusted summaries or a detailed account of event collection and attribution. The at-risk denominators for safety differ from the randomized group sizes, and the reason is not reported in the registry record. These limitations constrain interpretation to the specific posted summaries.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Efficacy and Safety of Pazopanib Monotherapy After First Line Chemotherapy in Ovarian, Fallopian Tube, or Primary Peritoneal Cancer — NCT00866697.
• Registry record last updated 2021-02-16; status last verified 2021-01.
• Results first posted 2013-12-19.
• 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

NCT00866697 is a completed randomized, double-masked phase III trial sponsored by Novartis Pharmaceuticals. It compared pazopanib 800 mg once daily with matched placebo, each administered orally for up to 24 months, in women with epithelial ovarian, fallopian tube, or primary peritoneal cancer whose disease had not progressed on first-line chemotherapy.

The primary outcome was investigator-assessed progression-free survival in the Intent-to-Treat population. The sponsor-reported hazard ratio was 0.766 (95% confidence interval 0.643 to 0.911; p = 0.002). The secondary overall-survival analysis reported a hazard ratio of 0.960 (95% confidence interval 0.805 to 1.145; p = 0.643). The registry also reports serious and other adverse-event summaries.

The record describes the endpoint definition and censoring rules but does not report the full statistical analysis plan, multiplicity strategy, original sample-size justification, or detailed missing-data procedures for all outcomes. These limits should inform interpretation of the posted results.