A Study to Assess Treatment With 2 Different Dosing Schedules of Trabectidin Administered to Patients With Advanced Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Assess Treatment With 2 Different Dosing Schedules of Trabectidin Administered to Patients With Advanced Cancer (NCT00060944), a randomized phase 2 study. The primary outcome is Time to Progression- Independent Review.

2. Clinical Question

The registry describes a randomized, multicenter, open-label, parallel-group study. It enrolled 271 participants and is recorded as completed. The question is a comparison between dosing schedules in the study population, not a comparison of trabectedin with no treatment or with another drug. Both groups received trabectedin, with different doses, infusion durations and treatment-cycle schedules; dexamethasone pretreatment also differed according to schedule.

The primary outcome was time to progression, and the registry also reports independent-review progression-free survival, objective response and overall survival. These outcomes address related but distinct questions. Time to progression focuses on documented progression or death due to progressive disease as defined in the record. Progression-free survival uses the same stated event definition, while overall survival concerns death. Objective response concerns the percentage of participants meeting the response outcome. The registry record does not report a separate question about the contribution of each drug or schedule component.

3. Trial Design

This was a phase 2 randomized study with a parallel-group design and no masking. The record describes it as multicenter and open-label. Participants were assigned to one of two trabectedin schedules: 1.5 mg/m2 as a 24-hour intravenous infusion once every 3 weeks, or 0.58 mg/m2 as a 3-hour intravenous infusion on Days 1, 8 and 15 of each 28-day cycle. Each schedule included dexamethasone pretreatment, at a different dose and frequency as described in the registry.

The record lists 271 participants enrolled. For the primary outcome, the stated population was all participants randomly assigned to either schedule, regardless of whether they received trabectedin. The posted arm counts for that outcome are 136 for the 1.5 mg/m2 schedule and 134 for the 0.58 mg/m2 schedule. The registry does not explain the relationship between the enrollment figure and these outcome-specific counts, so no reason for the difference should be inferred.

The primary outcome was time to progression assessed by independent review. Its timeframe is described as from randomization until the first documentation of disease progression or death due to progressive disease, whichever occurred first, assessed up to 5 years. The registry lists objective response, duration of response, progression-free survival and overall survival among the secondary outcomes. Results are posted for objective response, progression-free survival and overall survival; a result for duration of response is not reported in the registry record.

Recruitment began in 2003-05, primary completion was 2008-05, and the study status is completed. The original protocol’s sample-size justification, intended power and other design assumptions are not reported in the registry record. The planning illustrations based on the observed effect do not establish what assumptions were used when the study was designed.

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: In this study 271 participants were enrolled of which 270 participants (134 in the Trabectedin 1.5 mg/m2 group and 136 in the Trabectedin 0.58 mg/m2 group) were randomized as 1 participant was enrolled twice. Of these, 260 participants were treated with trabectedin including 130 participants in each treatment group.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: All participants who were randomly assigned to one of the two schedules, independent of whether they received trabectedin or not.

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 Time to Progression- Independent Review, measured over From randomization to the first documentation of disease progression or death due to progressive disease, whichever occurs first, assessed up to 5 years.

Time to progression measures the time from randomization until the first documentation of disease progression or death due to progressive disease, whichever occurs first. The registry specifies that progression was assessed by independent review and that follow-up for this outcome was assessed up to 5 years. The stated primary analysis population includes everyone randomly assigned to one of the two schedules, whether or not they received trabectedin.

This is a time-to-event outcome: the analysis concerns not only whether an event occurred, but also how long participants remained without the defined event during observation. In general, time-to-event methods can use information from participants whose event has not been observed by the end of their available follow-up, rather than treating their unobserved event time as if it were known. The registry record does not describe the specific handling of censoring or missing follow-up for this outcome.

The median is a summary of the event-time distribution: in general, it marks the time by which half of the analyzed population has experienced the event, under the method used to estimate the distribution. The posted medians are 3.7 months for the 1.5 mg/m2 schedule and 2.3 months for the 0.58 mg/m2 schedule. These summaries describe the observed time-to-progression distributions; they do not by themselves describe the full pattern over follow-up. The hazard ratio reported by the sponsor provides a comparative summary across event times, while its confidence interval conveys uncertainty around that estimate.

Time to progression is used to summarize how long participants remain without documented progression under the specified event definition. It is distinct from overall survival, which concerns death, and from objective response, which summarizes whether a response was recorded.

7. Results Posted in the Registry

• Trabectedin 1.5 mg/m2 vs Trabectedin 0.58 mg/m2: hazard ratio 0.73 (95% CI 0.55–0.97), reported p = 0.030 (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 Objective Response - Independent Review

• 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:
  • Trabectedin 0.58 mg/m2: 1.5% (2/134) versus 5.1% (7/136) on control; risk difference -3.7 percentage points (95% CI -7.9 to 0.6), risk ratio 0.29 (0.06–1.37); unadjusted two-proportion z-test p = 0.094.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Trabectedin 0.58 mg/m2 and the control. The interval gives the range of effects that remain compatible with the data.

Progression-Free Survival - Independent Review

• 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:
  • Trabectedin 1.5 mg/m2 vs Trabectedin 0.58 mg/m2: hazard ratio 0.76 (95% CI 0.57–0.99), reported p = 0.042 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Trabectedin 1.5 mg/m2 vs Trabectedin 0.58 mg/m2 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Overall Survival

• 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:
  • Trabectedin 1.5 mg/m2 vs Trabectedin 0.58 mg/m2: hazard ratio 0.84 (95% CI 0.65–1.09), reported p = 0.192 (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 Trabectedin 1.5 mg/m2 vs Trabectedin 0.58 mg/m2 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover response, progression-free survival and overall survival, with duration of response also named among the secondary outcomes. The posted time-to-event estimates for progression-free survival and overall survival have hazard ratios below 1 for the 1.5 mg/m2 schedule compared with the 0.58 mg/m2 schedule. The progression-free survival confidence interval does not include 1; the overall-survival confidence interval does. The objective-response percentages are small in both groups, and the registry does not report a sponsor analysis for that comparison. A duration-of-response result is not reported in the registry record.

These outcomes relate to, but do not duplicate, the primary time-to-progression result. Progression-free survival shares the registry’s stated event definition, whereas overall survival concerns death. Objective response asks whether a response was recorded rather than how long participants remained free of an event. Similar directions across some estimates can add context, but outcomes measure different features of participants’ courses and need not yield identical statistical evidence.

The primary outcome was designated as the main question, while the registry lists several secondary outcomes. When multiple outcomes are examined, the chance of obtaining at least one apparently notable result can increase. General: multiplicity procedures can control that concern by adjusting the testing strategy or interpreting secondary analyses as exploratory. Whether such procedures were used is not reported in the registry record. The secondary results therefore carry less weight as confirmatory evidence than a prespecified primary analysis, particularly when the analysis plan and multiplicity handling are unavailable.

The secondary estimates are best read as supporting context, not as independent confirmation that all outcomes differ between schedules. Confidence intervals, outcome definitions and the presence or absence of sponsor-reported analyses should be considered together. No result for duration of response should be inferred from the other secondary outcomes.

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

• Percentage of Participants Objective Response - Independent Review
• Duration of Response - Independent Review
• Progression-Free Survival - Independent Review
• Overall Survival

9. Statistical Interpretation

10. Statistical Methods Explained

What does the hazard ratio describe?

For the primary outcome, the sponsor reported a hazard ratio of 0.734 for trabectedin 1.5 mg/m2 versus 0.58 mg/m2. In general, a hazard ratio compares the rates at which events occur over follow-up between groups. A value below 1 indicates a lower event hazard in the first group relative to the second under the reported comparison and model. It is not a difference in median months, nor does it say that a particular fraction of participants avoided progression. The registry record does not describe the model details beyond the reported measure and Log Rank method.

What does the Log Rank method contribute?

The reported comparisons for the primary outcome and the time-to-event secondary outcomes used the Log Rank method. In general, the Log Rank test compares event-time patterns between groups while taking account of the timing of observed events and participants’ follow-up. It is designed for time-to-event data, unlike a comparison that treats each participant’s outcome as a simple yes-or-no status at one fixed time. The registry record does not state whether additional adjustments, such as stratification or covariate adjustment, were used.

How do the median and hazard ratio differ?

A median time summarizes the estimated distribution within a group. A hazard ratio summarizes a between-group comparison across follow-up. The primary medians are 3.7 months and 2.3 months, while the sponsor-reported hazard ratio is 0.734. These measures address the same broad event-time outcome but answer different statistical questions. Neither alone describes every feature of the distributions, and the hazard ratio should not be interpreted as a comparison of the medians themselves.

How should a confidence interval be read?

In general, a confidence interval expresses uncertainty in an estimate using a method with a stated coverage level. For the primary hazard ratio, the reported 95% confidence interval is 0.554 to 0.974. The interval gives a range of values compatible with the data and analysis under the method’s assumptions; it is not a range containing a known fraction of individual participant outcomes. A narrower interval generally indicates greater precision than a wider interval, though precision alone does not settle questions about study design, bias or applicability.

What does the p-value say?

The primary reported p-value is 0.030. In general, a p-value describes how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The registry record identifies the Log Rank method and reports the p-value, but the full testing plan and any handling of multiple outcomes are not reported in the registry record.

Why does independent review matter?

The primary outcome and some secondary outcomes are identified as assessed by independent review. In general, a review independent of the treatment team can help separate outcome assessment from knowledge of treatment assignment. This trial was open-label, so masking was absent; the record does not describe review procedures, reviewer masking, disagreements or how assessments were adjudicated. Independent review is therefore part of the outcome description, but the registry record does not provide enough detail to evaluate all aspects of its implementation.

Why does over-dispersion matter?

General: over-dispersion occurs when the variability in data is greater than a statistical model expects. If a model assumes less variability than is present, its uncertainty estimates can be too small, making confidence intervals appear overly narrow and tests appear more decisive than warranted. This is a general issue in some count or grouped-outcome analyses. The primary outcome is time-to-event, and the registry record does not report an over-dispersion assessment or identify it as a concern. No conclusion about over-dispersion can be drawn from the posted time-to-event results alone.

The objective-response result is a binary outcome, meaning each participant is classified according to whether a response was recorded. General: binary outcomes are often compared using a difference in proportions, a relative measure, or a model-based test. The posted response comparison includes an unadjusted risk difference and a p-value, but the registry record does not list a sponsor-reported analysis for this outcome. The posted percentages and their confidence intervals are descriptive of the response estimates; they do not replace the sponsor-reported primary time-to-event analysis.

11. Confidence Intervals and Precision

The primary median time to progression is reported as 3.7 months for the 1.5 mg/m2 schedule, with a 95% confidence interval from 2.1 to 5.4 months. For the 0.58 mg/m2 schedule, the median is 2.3 months, with a 95% confidence interval from 2.0 to 3.5 months. These intervals convey uncertainty in the estimated median for each group. Their overlap does not by itself determine the result of a between-group test; the reported comparison is the hazard ratio with its own confidence interval and p-value.

The sponsor-reported primary hazard ratio is 0.734, with a 95% confidence interval from 0.554 to 0.974. The interval lies below 1, indicating that values at 1 are not included in the reported interval under the analysis method. Its upper limit is close to 1, so the estimated comparative effect is not known with high precision. The interval also contains a range of possible relative hazard estimates, rather than identifying a single exact value.

In general, confidence intervals reflect both the observed data and assumptions of the statistical method. They do not account automatically for every possible source of uncertainty, including unreported analysis choices, missing data or multiplicity. The registry record does not give enough detail to assess all such sources. The sample sizes and event counts used in the time-to-event estimates are not fully described in the posted results, beyond the outcome-specific participant counts.

Precision should be considered alongside the point estimate, the outcome definition, the analysis population and the trial design. The primary result is more informative than a median alone because it includes a reported comparative estimate and uncertainty interval. At the same time, the interval’s width and the limits of the registry entries counsel against treating the estimate as exact or assuming it will transfer unchanged to other settings.

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 translate observed effects into hypothetical sample-size requirements; they are not the original trial’s design calculation. For time-to-event outcomes, the figures are total events required across groups, not participants per arm. For the binary objective-response outcome, the figures are participants per arm. Each effect scenario considers the full observed effect or a stated fraction of it. A smaller effect is harder to distinguish from random variation and therefore requires more participants or, for time-to-event outcomes, more events.

The calculations use a two-sided significance level 0.05, equal allocation between the two arms and a normal approximation. The effect to detect is the stated fraction of the observed effect. The 80% power column represents the planned chance of detecting an effect of that size under the assumptions if the effect is present; the 90% power column represents a higher planned chance of detection under those same assumptions. These are design-planning concepts, not guarantees about a future study.

For example, the primary time-to-progression illustration at 100% of the observed effect gives 329 total events for 80% power and 440 total events for 90% power. At 75% of the observed effect, the corresponding requirements are 584 and 782 total events. For the objective-response comparison, the 100% scenario gives 377 participants per arm for 80% power and 503 participants per arm for 90% power. The full set of effect scenarios gives the numerical detail for the other planning levels.

These figures are not observed power. They are planning illustrations computed from the observed effect, not evidence about the probability that the completed trial detected an effect. The registry record does not report the study’s original sample-size justification or design assumptions.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

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 = 0.734, so ln(HR) = -0.3092.
2. d = 4 × (1.96 + 0.842)² / [ln(0.734)]² = 328.3, rounded up to 329 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 <- 0.734                              # 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(60944)
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 = 329 (80% power), 440 (90% power)
 75% of observed effect: events = 584 (80% power), 782 (90% power)
 50% of observed effect: events = 1,314 (80% power), 1,758 (90% power)
Simulated power with 329 events: 0.790 (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 462 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 271 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 <- 2.3          # control-arm median, months (converted from the posted unit)
hr          <- 0.734          # 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: 224         p (1-sided)   0.0001
 Events: 149        ~HR at bound   0.5435
   Month: 12    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.73   0.0338
   IA 2: 67%                   Z   2.5114
      N: 380         p (1-sided)   0.0060
 Events: 297        ~HR at bound   0.7469
   Month: 20    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.73   0.5603
       Final                   Z   1.9930
      N: 462         p (1-sided)   0.0231
 Events: 445        ~HR at bound   0.8277
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.73   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-reported primary analysis used the Log Rank method and gave a hazard ratio of 0.734, a 95% confidence interval from 0.554 to 0.974, and p = 0.030. The posted comparison is consistent with the sponsor’s reported result; the registry record does not indicate a discrepancy. The sponsor’s analysis is the primary reference for interpreting this time-to-event comparison, rather than an unadjusted recalculation from summary statistics.

The registry also reports sponsor analyses for progression-free survival and overall survival. Those analyses use the Log Rank method and report hazard ratios, confidence intervals and p-values. They should be distinguished from calculations reconstructed from group-level summaries. In general, such recalculations can be useful checks or supplementary descriptions, but they may not reproduce the full analysis because they lack participant-level event times and details of the original analysis procedures.

For objective response, a comparison can be recalculated from the posted counts and group sizes, but the registry record does not list a sponsor-reported analysis for that outcome. The recalculated comparison is unadjusted and should be read as a supplementary estimate, not as a replacement for a sponsor analysis. The registry record does not report enough information to establish whether an unposted analysis was performed or how it might have differed.

The distinction is important: sponsor-reported analyses reflect the analysis identified in the registry, while recalculations from summary data depend on simplified assumptions and available aggregate information. Neither distinction resolves limitations in the reporting record, including unreported details of the analysis plan.

16. Multiplicity, Missing Data and Analysis Populations

The primary analysis population is explicitly described as all participants randomly assigned to one of the two schedules, irrespective of whether they received trabectedin. This resembles an intention-to-treat population description, but the registry record does not give further detail about exclusions or the exact analysis set used. The endpoint results list 136 participants for the 1.5 mg/m2 schedule and 134 for the 0.58 mg/m2 schedule. The record does not explain why those counts differ from the overall enrollment figure.

The registry names multiple outcomes, including the primary time-to-progression outcome and several secondary outcomes. Whether the statistical testing plan adjusted for multiple comparisons, ordered the outcomes hierarchically or treated some analyses as exploratory is not reported in the registry record. Without that information, individual secondary p-values should not be interpreted as if each were the only hypothesis tested.

Details of missing outcome data, loss to follow-up, censoring rules and sensitivity analyses are not reported in the registry record. For a time-to-event outcome, those details matter because participants may have different lengths of observed follow-up and may not experience the event during observation. General: time-to-event analyses commonly account for such incomplete event-time information through censoring, but the specific procedures used in this study cannot be established from the registry information.

The registry record also does not report interim analyses, stopping rules, the original statistical analysis plan or the original sample-size justification. Those omissions limit evaluation of how the analysis was planned, whether the posted outcome results reflect all intended analyses and how protocol decisions may have affected interpretation. The listed primary outcome and sponsor-reported method remain interpretable as posted, but the missing details restrict a fuller assessment of robustness and multiplicity.

17. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

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: abdominal pain (5.4%), pneumonia (4.6%), pyrexia (3.8%), deep vein thrombosis (3.8%), cardiac failure congestive (2.3%).

The serious adverse event figures list 130 participants at risk in each schedule group. Serious adverse events affected 48 participants in the 1.5 mg/m2 group and 41 in the 0.58 mg/m2 group. The separate figures for participants at risk of other adverse events are also 130 in each group; other adverse events affected 129 and 128 participants, respectively. These are posted counts, not a direct comparison adjusted for exposure time or other factors.

The most frequent serious adverse event terms listed include abdominal pain at 5.4%, pneumonia at 4.6%, pyrexia at 3.8%, deep vein thrombosis at 3.8%, congestive cardiac failure at 2.3% and intestinal obstruction at 2.3%. The registry record does not provide enough detail in these figures to determine the timing, duration, severity distribution beyond the serious-event designation, or attribution of each event to treatment. Death counts are not reported in the registry record.

These safety figures describe events recorded in the study and should be read separately from the efficacy outcomes. Differences in counts alone do not establish a cause or a comparative risk, particularly without additional information about exposure, event definitions and analysis methods. They also do not support conclusions about safety outside the participants and follow-up represented in the registry record.

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

The posted primary result indicates that the sponsor’s time-to-progression analysis favored the 1.5 mg/m2 schedule in its comparison with the 0.58 mg/m2 schedule: the reported hazard ratio is 0.734, its 95% confidence interval is 0.554 to 0.974, and the p-value is 0.030. The group medians are 3.7 months and 2.3 months, respectively. These statistics describe the observed randomized comparison and its uncertainty under the reported analysis.

They do not establish the exact effect for every participant, nor do they prove that the same estimate applies to other populations or treatment settings. The hazard ratio is a group-level time-to-event summary, not an individual prediction or a direct comparison of medians. The confidence interval indicates uncertainty, and the available registry description does not resolve all possible limitations in follow-up, missing data or analytic choices.

The trial compared two complete treatment schedules, including different trabectedin doses, infusion durations, cycle timing and dexamethasone pretreatment. It cannot isolate which of those differences accounts for the observed result. There was no untreated comparator in the described design, so the results address the relative schedules rather than the effect of trabectedin compared with no treatment.

The secondary results offer additional context, but they do not all provide the same degree of statistical evidence and multiplicity handling is not reported. The posted safety counts describe observed events but do not, by themselves, establish attribution or comparative risk. Overall, the record supports a careful description of the reported comparison, not a broad claim about treatment effects beyond the study’s population, schedules, outcome definitions and analysis.

19. Why This Trial Matters Statistically

This trial illustrates several issues that arise when interpreting a randomized comparison of treatment schedules. Although both groups received the same named drug, the schedules differed in dose, infusion duration and treatment-cycle timing; dexamethasone pretreatment also differed. The result therefore concerns the schedules as implemented, rather than a single isolated dosing feature.

It also demonstrates why a time-to-event endpoint is not fully represented by a pair of medians. The registry reports group medians as well as a sponsor-reported hazard ratio, confidence interval and Log Rank p-value. Together, these describe different aspects of the event-time data: group-level timing, comparative event hazard and uncertainty under the reported analysis. None of these alone gives a complete account of every participant’s outcome or the full shape of follow-up.

The distinction between a primary outcome and multiple secondary outcomes is another important statistical lesson. Secondary findings can provide context, but several outcomes create a multiplicity concern, and the registry record does not state whether an adjustment or testing hierarchy was used. The contrast between sponsor-reported time-to-event analyses and an unadjusted recalculation for objective response also shows why the source and method of an estimate matter.

Finally, planning illustrations based on observed effects should not be mistaken for the trial’s original design rationale or for observed power. The original sample-size assumptions are not reported in the registry record. Keeping planning calculations, sponsor analyses and secondary exploratory comparisons distinct helps prevent stronger conclusions than the available statistical record supports.

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 contains limited detail about the statistical plan. It does not report the original sample-size justification, planned power, interim analyses, stopping rules or whether multiplicity was addressed. These omissions make it difficult to assess how the primary and secondary analyses were prespecified and how the number of outcomes affected interpretation.

Although the primary population is described as all randomized participants regardless of treatment receipt, the registry does not provide detailed accounting of exclusions, missing observations, loss to follow-up or censoring. It also does not report sensitivity analyses for these issues. The reported outcome-specific participant counts are not reconciled with the overall enrollment figure.

The study was open-label, and the registry does not describe the independent review process in detail. It identifies independent review for the primary outcome and certain secondary outcomes, but does not state whether reviewers were masked to assignment, how disagreements were resolved or how assessments were adjudicated. The record also does not report a proportional-hazards assessment or other model diagnostics for the hazard-ratio analyses.

The comparison is between two schedules that differ in more than one feature, including dose, infusion duration and cycle schedule, as well as dexamethasone pretreatment. The design therefore does not isolate the role of each component. The record provides no untreated or alternative-drug comparator. Safety reporting includes counts and selected serious-event terms, but the listed details do not establish treatment attribution or account for exposure duration. A duration-of-response result is not reported in the registry record.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study to Assess Treatment With 2 Different Dosing Schedules of Trabectidin Administered to Patients With Advanced Cancer — NCT00060944.
• Registry record last updated 2014-09-08; status last verified 2014-08.
• Results first posted 2014-09-08.
• 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

The registry describes a completed, randomized, multicenter, open-label phase 2 parallel-group study of two trabectedin schedules in participants with locally advanced or metastatic liposarcoma or leiomyosarcoma following anthracycline and ifosfamide treatment. Enrollment was 271. Recruitment began in 2003-05 and primary completion was 2008-05.

The primary outcome was time to progression assessed by independent review. The sponsor reported a Log Rank hazard ratio of 0.734 for trabectedin 1.5 mg/m2 versus 0.58 mg/m2, with a 95% confidence interval from 0.554 to 0.974 and p = 0.030. Secondary results include progression-free survival, overall survival and objective response. The record does not report a result for duration of response.

Important design and analysis details—including the original sample-size justification, multiplicity approach, missing-data handling and interim analyses—are not reported in the registry record.