Combination Chemotherapy With or Without Temsirolimus in Treating Patients With Intermediate Risk Rhabdomyosarcoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Combination Chemotherapy With or Without Temsirolimus in Treating Patients With Intermediate Risk Rhabdomyosarcoma (NCT02567435), a randomized phase 3 study. The primary outcome is Event-free Survival (EFS).

2. Clinical Question

3. Trial Design

This is a randomized, phase 3, parallel-group trial with no masking. The registry lists enrollment of 325 and identifies the National Cancer Institute as sponsor. The study start is recorded as 2016-06-01, primary completion as 2023-06-30, and status as active, not recruiting. The planned primary follow-up timeframe is up to 3 years from study entry.

The principal comparison is between Regimen A, VAC/VI, and Regimen B, VAC/VI plus temsirolimus. Both regimens include vincristine, dactinomycin, and cyclophosphamide; the listed experimental regimen adds temsirolimus. The arm descriptions give administration schedules for the chemotherapy components. The registry summary describes the study as comparing combination chemotherapy with combination chemotherapy plus temsirolimus in intermediate-risk rhabdomyosarcoma.

The primary analysis is described as including patients randomized to Regimen A and Regimen B, using a revised intention-to-treat approach. The registry also says that 4 ineligible patients and 11 feasibility patients were excluded, followed by an additional exclusion phrase that is not reported in the registry record in complete form. Thus, the stated enrollment and the analysis denominators refer to different stages of the trial record and should not be treated as interchangeable.

The registry lists a separate FOXO1 fusion-negative VAC/VA regimen and a feasibility VAC/VI/temsirolimus group in the treatment and safety information. Their role in the broader study is not fully described in the reported primary comparison. Details of allocation concealment, stratification, the trial's original sample-size justification, and any interim analyses are not reported in the registry record.

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: Among the 325 patients that enrolled, 4 patients were ineligible, 11 eligible patients were enrolled onto the feasibility phase (with 1 transferred to Regimen C), and 310 eligible patients were randomized and enrolled onto the efficacy phase (with 2 transferred to Regimen C). 13 randomized eligible patients were not analyzed (not evaluable due to FOXO1 diagnosis or amendment after study activated).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: As pre-specified in the protocol, patients randomized to Regimen A (VAC/VI) and Regimen B (VAC/VI/Temsirolimus) were included in this analysis. The data was analyzed with revised intention-to-treat approach. Following patients were excluded 4 ineligible patients, 11 feasibility patients and 13 inevaluable patients (due to FOXO1 results or who did not receive maintenance therapy due to an amendment added during the study) .

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 Event-free Survival (EFS), measured over Up to 3 years from study entry.

The primary endpoint is event-free survival (EFS), reported as a percentage of participants at 3 years from study entry. An EFS event is the first occurrence of progression, relapse, a second malignancy, or death. EFS therefore combines several clinically relevant ways in which a participant may experience an unfavorable event, rather than measuring only death.

The registry specifies a Kaplan-Meier estimate and a log-rank comparison between the randomized treatment groups. In general, time-to-event outcomes use both the timing of events and the follow-up available for participants. Kaplan-Meier estimation is commonly used when participants have different follow-up durations; it can incorporate information up to the last known follow-up for those without a recorded event. Whether particular censoring decisions or event-adjudication procedures were used is not reported in the registry record.

EFS is useful for comparing how long participants remain free of the defined events, but it is not identical to overall survival. The event definition includes progression and relapse as well as death, so the endpoint reflects a broader set of outcomes. The registry also reports overall survival as a secondary outcome. The primary endpoint’s interpretation should remain tied to its stated event definition, timeframe, randomized groups, and reported analysis.

7. Results Posted in the Registry

• Regimen B (VAC/VI/Temsirolimus): 67.1% (100/149) versus 64.9% (96/148) on control; risk difference 2.2 percentage points (95% CI -8.5 to 13.0), risk ratio 1.03 (0.88–1.22); unadjusted two-proportion z-test p = 0.682.

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 (OS)

• 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:
  • Regimen B (VAC/VI/Temsirolimus): 77.9% (116/149) versus 78.4% (116/148) on control; risk difference -0.5 percentage points (95% CI -9.9 to 8.9), risk ratio 0.99 (0.88–1.12); unadjusted two-proportion z-test p = 0.913.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Regimen B (VAC/VI/Temsirolimus) and the control. The interval gives the range of effects that remain compatible with the data.

Overall survival is the one secondary outcome posted. The registry reports group-level estimates and uncertainty for OS, and the sponsor reports a log-rank comparison with 3-Year OS of 78.2% and p = 0.56. The pattern is broadly consistent with the primary result in that the posted sponsor analyses do not show a statistically clear separation between the randomized groups. However, the endpoints measure different outcomes: EFS includes progression, relapse, second malignancy, or death, whereas OS concerns survival.

OS is secondary rather than the primary question. A secondary result can add context, but it does not supersede the primary EFS analysis or change its interpretation. It also should not be treated as independent confirmation of the primary result without considering the analysis plan and the relationship between endpoints. The registry does not report whether the secondary analysis was designated as confirmatory or whether any multiplicity adjustment was used.

When several outcomes or comparisons are examined, the chance of observing a seemingly notable result by chance can increase. In general, unadjusted secondary tests do not account for that multiplicity, so their p-values carry less confirmatory weight than a prespecified primary test. The registry reports one secondary outcome and does not describe a correction strategy. No additional secondary endpoint results are posted in the record.

The secondary outcome should therefore be read as supportive descriptive information, with its own uncertainty and analysis limitations. It does not establish that the treatments are equivalent, and it does not resolve the incomplete reporting of the primary comparison's confidence interval, analysis details, or missing-data procedures.

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

• Overall Survival (OS)

9. Statistical Interpretation

10. Statistical Methods Explained

The registry describes the primary EFS estimate as a Kaplan-Meier analysis, with the log-rank test comparing the randomized groups. The posted values are time-to-event results, not simple proportions calculated by dividing the number of participants with an event by the number enrolled. That distinction matters because participants may have different lengths of follow-up and because the endpoint is defined by the time until the first qualifying event.

What does Kaplan-Meier estimation do?

In general, Kaplan-Meier estimation describes the probability of remaining free of an event over time. At each event time, it updates the estimated event-free proportion using the participants still under observation at that time. A participant who has no recorded event before their last follow-up may contribute information until that point without being treated as if an event occurred. This is a general explanation of the method; details of how censoring and follow-up were handled in this trial are not reported in the registry record.

The reported EFS percentage at the stated timeframe is an estimate from that event-time analysis. It should not be interpreted as a raw percentage of participants who never experienced an event throughout all possible follow-up. The primary result is framed as EFS up to 3 years from study entry, and the sponsor describes use of the Kaplan-Meier method to estimate 3-year EFS for the randomized treatment groups.

What does the log-rank test compare?

In general, the log-rank test compares the event-time experience of groups across the follow-up period. It uses the timing of events and the numbers still at risk over time, rather than comparing only the endpoint percentages. The sponsor reports this method for the Regimen A versus Regimen B comparison and gives p = 0.44 for 3-Year EFS. A p-value summarizes how compatible the observed data are with a specified no-difference model under the test assumptions. It is not the chance that the null hypothesis is true, and it does not measure the size or clinical importance of a difference.

The registry does not provide the assumptions or diagnostics used for the log-rank analysis, such as an assessment of whether differences between groups vary over time. It also does not report a confidence interval alongside the sponsor's 3-Year EFS result. Those omissions make it harder to evaluate the precision and robustness of the sponsor's time-to-event comparison using the registry record alone.

How does the recalculation differ?

The posted recalculation is an unadjusted comparison based on summary counts. It reports a risk difference of 0.022, a 95% confidence interval from -0.085 to 0.130, and p = 0.682 for Regimen B relative to Regimen A. In general, a risk difference expresses the difference between two event proportions in the analyzed groups. The recalculation is simpler than a time-to-event analysis: it does not reproduce the Kaplan-Meier estimates or the log-rank test, and it does not use event timing in the same way. It is useful as a secondary view of the posted counts, but it should not be confused with the sponsor's primary analysis.

The arm-level EFS estimates and confidence intervals are reported as percentages, while the recalculated comparison is represented as a risk difference. These are related summaries of the comparison, but they arise from different calculations and should be read according to their stated methods. The registry marks no discrepancy between the posted comparison and its reported results.

What does a confidence interval communicate?

In general, a confidence interval describes statistical uncertainty around an estimate under the method used to construct it. A wider interval indicates less precision than a narrower interval, all else being equal. The intervals around the two EFS estimates show that the point estimates are not known exactly. They do not give the range in which every participant's outcome lies, nor do they assign a probability to a particular treatment effect after observing the data.

Confidence intervals for separate group estimates are not a substitute for a confidence interval on the contrast between groups. The recalculated risk-difference interval directly describes uncertainty in that unadjusted contrast. The sponsor's log-rank p-value answers a different question and is not accompanied by a contrast interval in the registry record.

What is not described?

The registry record does not report a complete statistical analysis plan, the original sample-size assumptions, allocation concealment procedures, interim-analysis procedures, missing-data methods, or adjustment for multiplicity. It identifies a revised intention-to-treat approach and gives a partial description of exclusions, but the full exclusion wording is not reported in the registry record. These details would help readers assess which participants contributed to each analysis and how the reported estimates were selected and interpreted.

11. Confidence Intervals and Precision

The 3-year EFS estimates are 64.8% for Regimen A, with a 95% confidence interval from 55.5% to 74.1%, and 66.8% for Regimen B, with a 95% confidence interval from 57.5% to 76.2%. These intervals express uncertainty around each group estimate. They span a range of values, rather than identifying the exact EFS percentage that would apply to every participant or setting.

The sponsor's log-rank result reports p = 0.44 but no confidence interval for the comparison. A p-value does not show the precision of the estimated treatment contrast or indicate which effect sizes remain compatible with the data. The registry record therefore leaves an important part of the uncertainty around the sponsor's primary comparison unquantified.

The unadjusted recalculation gives a risk difference of 0.022, with a 95% confidence interval from -0.085 to 0.130. This interval includes values on both sides of zero, so the recalculation is compatible with a range of possible directions and magnitudes under its method. It remains a simple analysis of summary counts and should not be read as the sponsor's time-to-event estimate.

In general, a confidence interval's width reflects both the amount of information and variability in the data, as well as the method used. A confidence interval is not a guarantee that the true value lies within its endpoints, and it does not capture every source of uncertainty, including limitations in outcome measurement or analysis choices. The registry does not report all details needed to assess those other sources of uncertainty.

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 calculations. For these time-to-event outcomes, the figures refer to the total number of events, as specified by the planning assumptions; they are not 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 use the stated fraction of the observed effect as the effect to detect. The original trial design assumptions are not reported in the registry record.

The 80% power column describes the number of events that a hypothetical study would need under those assumptions for an 80% chance of detecting the chosen effect at the stated significance level, if that effect were real and the assumptions held. The 90% power column describes the corresponding planning target for a 90% chance. These are design-planning quantities, not probabilities that the observed result is true and not estimates of the trial's achieved power.

The planning rows consider the full observed effect, 75% of the observed effect, and 50% of the observed effect. A smaller target effect is harder to distinguish from random variation, so the planning illustration requires more events to reach the same power target. This explains why the figures rise as the assumed fraction of the observed effect falls.

These calculations are based on the observed effect and are not the trial's own sample-size justification. They should not be used to infer that the trial was adequately or inadequately powered: the original design assumptions and target effect are not reported in the registry record. The figures are prospective planning illustrations, not observed power and not a retrospective measure of the strength of evidence.

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 = 0.649; treatment proportion p₁ = 0.671; average p̄ = 0.660.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6700 = 1.3131.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6698 = 0.5637.
4. n = (1.3131 + 0.5637)² / (0.0225)² = 6,962.8, rounded up to 6,963 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 <- 0.648648648648649                          # control proportion
p1 <- 0.671140939597315                          # 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(2567435)
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 = 6,963 (80% power), 9,321 (90% power)
 75% of observed effect: n per arm = 12,429 (80% power), 16,638 (90% power)
 50% of observed effect: n per arm = 28,075 (80% power), 37,583 (90% power)
power.prop.test: 6962.8 
Simulated power at n = 6,963 per arm: 0.795 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor's primary EFS analysis is a log-rank comparison of the randomized groups, reporting 3-Year EFS of 65.8% and p = 0.44. The registry separately posts arm-specific Kaplan-Meier estimates and a simple recalculation based on summary counts. The recalculated risk difference is 0.022, with a 95% confidence interval from -0.085 to 0.130 and p = 0.682.

These analyses are not identical. The sponsor's method compares time-to-event experience, while the recalculation treats the posted counts as summary proportions and does not reproduce the Kaplan-Meier or log-rank analysis. Their estimates and p-values need not match because they use different summaries and methods. The sponsor analysis addresses the stated primary endpoint in the way described in the registry; the recalculation is supplementary and should not replace it.

The registry marks the discrepancy flag as false. The original design and analysis plan, beyond the method summary in the record, are not reported in the registry record. The registry also does not provide a confidence interval for the sponsor's log-rank comparison. Consequently, the recalculated interval offers an uncertainty measure for its own simple contrast, but it does not fill in the missing interval for the sponsor's time-to-event result.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies EFS as the primary endpoint and OS as a secondary outcome, but it does not report a multiplicity strategy. It is therefore not reported in the registry record whether secondary tests were adjusted for multiple comparisons, whether any hierarchy among outcomes was prespecified, or whether other planned analyses were conducted. In general, testing multiple outcomes without adjustment can make isolated statistically notable findings less persuasive because the chance of a chance finding grows as more tests are considered.

The primary analysis population is described as a revised intention-to-treat population of patients randomized to Regimen A and Regimen B. The registry lists exclusions of 4 ineligible patients and 11 feasibility patients, followed by incomplete exclusion wording. The complete set of exclusions and the precise implications of the revised approach are not reported in the registry record. Readers should not assume that the posted analysis includes every randomized participant solely from the intention-to-treat label.

Missing outcome data, loss to follow-up, censoring rules, and methods for handling incomplete follow-up are not reported in the registry record. For a time-to-event endpoint, the handling of follow-up and censoring can affect how much information contributes to the estimated event-free experience. The registry identifies Kaplan-Meier estimation and a log-rank test but does not provide enough detail to evaluate those data-handling decisions.

The record also does not report a complete protocol-level statistical analysis plan, interim analyses, stopping rules, allocation concealment, or the original sample-size assumptions. These omissions do not demonstrate that such procedures were absent; they mean that they are not reported in the registry record. They limit independent assessment of analysis choices, planned comparisons, and the relationship between the reported results and the original study plan.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: mucositis oral (22.9%), anaphylaxis (10.0%), dehydration (10.0%), dermatitis radiation (10.0%), diarrhea (10.0%).

The safety record gives serious adverse event counts and the number at risk for four listed groups. For Regimen A, 17 serious adverse events are reported among 155 at risk; for Regimen B, 77 are reported among 153 at risk. The FOXO1 fusion-negative VAC/VA group has 0 among 3 at risk, and the feasibility VAC/VI/temsirolimus group has 6 among 10 at risk. These are the registry's serious-event figures; they should be read with their group labels and denominators rather than combined across groups.

The record also reports other adverse event counts and deaths for these groups. Those counts are not equivalent to a treatment-attributable death count, and the registry summary does not establish causation. The listed serious adverse event terms include oral mucositis at 22.9%, with anaphylaxis, dehydration, radiation dermatitis, diarrhea, and hyponatremia each listed at 10.0%. The registry information does not provide enough detail to infer duration, recurrence, severity grading, or how those terms were distributed across the randomized groups.

Safety counts can be affected by the population monitored, exposure time, event definitions, and reporting period. These details are not reported in the registry record. The separate regimen and feasibility groups should not be treated as part of the primary randomized efficacy comparison.

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

The results describe a randomized comparison of VAC/VI with VAC/VI plus temsirolimus for intermediate-risk rhabdomyosarcoma. The primary endpoint is 3-year EFS, with events defined as progression, relapse, a second malignancy, or death. The posted sponsor analysis reports a log-rank p-value of 0.44. The arm estimates and recalculated contrast show uncertainty, and the sponsor result does not provide a confidence interval for the comparison.

These findings do not prove that the two regimens have exactly the same effect. A lack of a statistically clear difference is not proof of equivalence or noninferiority. Such conclusions require a prespecified design and margin, neither of which is reported in the registry record. Similarly, the results do not establish that one regimen is superior. The reported estimates should be understood as evidence from the participants and follow-up contributing to these analyses, with the limitations of the posted methods and reporting.

The endpoint also matters. EFS includes several types of events and is not the same as overall survival. The secondary OS result provides a separate view of survival, but it does not replace the primary endpoint. Neither endpoint alone summarizes every outcome that might matter to patients or clinicians, and the registry's posted results do not address outcomes beyond those reported.

The registry record does not report the complete statistical analysis plan, missing-data procedures, multiplicity adjustment, or full analysis-population details. As a result, the posted numbers cannot answer every question about robustness or generalizability. They also do not establish how the estimates apply to patients outside the trial population or to different treatment settings. The appropriate statistical reading is bounded: describe the estimates, their stated uncertainty, and the analyses reported, without turning an inconclusive comparison into proof of no effect or a claim of benefit.

18. Why This Trial Matters Statistically

This trial poses a clear statistical comparison: two randomized regimens are assessed using a time-to-event primary endpoint. Its design allows the study to compare EFS between the assigned groups while accounting for event timing, rather than relying solely on a count at a single follow-up point. The defined endpoint combines progression, relapse, second malignancy, and death, making the outcome broader than survival alone.

The example also shows why the analysis method matters. The sponsor's log-rank result and the simple recalculation are based on different approaches. The recalculation can provide a straightforward view of posted summary counts, but it does not reproduce the time-to-event analysis. Readers need to distinguish a supplementary unadjusted contrast from the sponsor's stated primary analysis rather than selecting one result as if the methods were interchangeable.

Precision is central to interpreting the findings. The group EFS estimates have confidence intervals, while the sponsor's log-rank comparison does not have a reported contrast interval in the registry record. The unadjusted recalculation does include a contrast interval, but it answers a different statistical question. Recognizing these distinctions helps prevent a p-value from being treated as a measure of effect size or certainty.

The registry also illustrates the importance of complete reporting. Details about missing data, multiplicity, the original sample-size rationale, and the full analysis population would help readers judge how the analyses were planned and how the estimates should be generalized. Transparent reporting of these methods is part of interpreting clinical trial evidence, not a technical afterthought.

19. Limitations

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

The registry record leaves important trial-specific analysis details unreported. The original sample-size assumptions and justification are not given, and the planning illustrations based on the observed effect are not a substitute for that design rationale. Interim analyses, stopping rules, allocation concealment, and a complete statistical analysis plan are also not reported in the registry record.

The primary population description states that a revised intention-to-treat approach was used and lists exclusions, but the final exclusion wording is incomplete. The record does not report full details of missing follow-up, censoring, or the handling of incomplete outcome data. It is therefore difficult to assess from the registry alone exactly how all participants contributed to the time-to-event estimates.

The sponsor's primary log-rank result has no reported confidence interval for the between-group comparison. The recalculated risk difference does have an interval, but it is an unadjusted summary-count analysis and is not a replacement for the time-to-event analysis. The registry also does not report a multiplicity adjustment for the secondary outcome.

The safety information includes Regimen C and feasibility groups in addition to the two randomized efficacy groups. Those groups should not be conflated with the primary comparison. Event definitions, observation windows, and attribution details are not reported in the registry record, limiting interpretation of the safety counts. Detailed eligibility criteria, participant characteristics, and the extent to which the analyzed population represents other settings are also not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Combination Chemotherapy With or Without Temsirolimus in Treating Patients With Intermediate Risk Rhabdomyosarcoma — NCT02567435.
• Registry record last updated 2026-10-01; status last verified 2026-04.
• Results first posted 2024-10-01.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT02567435 is a randomized, open-label, phase 3 parallel-group study sponsored by the National Cancer Institute. It compares VAC/VI with VAC/VI plus temsirolimus in patients with intermediate-risk rhabdomyosarcoma. The registry lists enrollment of 325 and an active, not recruiting status.

The primary endpoint is 3-year EFS, defined by progression, relapse, second malignancy, or death. The sponsor reports a log-rank analysis with 3-Year EFS of 65.8% and p = 0.44. The registry also posts arm-level estimates, confidence intervals, a simple unadjusted recalculation, OS as a secondary outcome, and adverse event information.

The findings should be read with the distinction between the sponsor's time-to-event analysis and the supplementary recalculation in mind. Important details about the original design assumptions, missing data, multiplicity, and the complete analysis population are not reported in the registry record.