Temozolomide, Cixutumumab, and Combination Chemotherapy in Treating Patients With Metastatic Rhabdomyosarcoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Temozolomide, Cixutumumab, and Combination Chemotherapy in Treating Patients With Metastatic Rhabdomyosarcoma (NCT01055314), a randomized phase 2 study. The primary outcome is Incidence of Adverse Events Assessed by Common Terminology Criteria for Adverse Events Version 4.0.

2. Clinical Question

3. Trial Design

The registry record describes a randomized, parallel-group phase 2 pilot study with no masking. It enrolled 175 participants and is marked completed. The listed study period began in 2010-01, and primary completion was recorded as 2016-06. The sponsor was the National Cancer Institute (NCI). The record does not report the original protocol’s detailed sample-size justification or its full allocation procedures.

Both groups received combination chemotherapy and radiation therapy. The first group is described as receiving cixutumumab, and the second as receiving temozolomide. The second arm description names vincristine sulfate, irinotecan hydrochloride, ifosfamide, etoposide, doxorubicin hydrochloride, cyclophosphamide, and dactinomycin, in addition to temozolomide and radiation therapy. The first arm description is incomplete in the registry record, so its full schedule cannot be reconstructed from that text.

For the primary outcome, the analysis population is described as excluding 9 participants who were ineligible or did not receive treatment. The arm counts for that outcome are 96 for IMC-A12 and 70 for temozolomide. The registry’s overall enrollment and the outcome-specific population are distinct quantities; the posted record does not give further detail about the disposition of every participant.

The primary endpoint was the number of participants with grade 3 or higher adverse events during therapy, with a timeframe of up to 54 weeks. Response rate (CR + PR) was also posted as a secondary outcome, assessed from treatment start through a maximum of 2 cycles, with each cycle described as 21 days, in the absence of progression or unacceptable toxicity. The registry record does not report a detailed statistical analysis plan, the randomization method, or whether any interim analyses were planned.

4. Participant Flow and Accounting

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

Before assignment: The number of participants started is 175. Eight patients were declared ineligible by the study chair, and one patient didn't receive treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: 18 participants were excluded because of ineligibility or insufficient information to assess feasibility.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: 175 patients were enrolled on the study.

6. Primary Endpoint

The registry lists the primary outcome as Incidence of Adverse Events Assessed by Common Terminology Criteria for Adverse Events Version 4.0, measured over Up to 54 weeks.

The primary endpoint counts participants who experienced grade 3 or higher adverse events during therapy, up to 54 weeks. The registry defines grade 3 as severe and undesirable, grade 4 as life-threatening or disabling, and grade 5 as death related to an adverse event. The combined grade 3+ category therefore includes events across these three severity grades. The endpoint is a participant count, not a count of every individual event: a participant with more than one qualifying event still contributes as a participant with an event.

Counting participants with serious treatment-emergent events is one way to describe the safety burden observed during a trial. It gives a direct account of how many people in each group had at least one event meeting the stated severity threshold. It does not, on its own, describe event duration, recurrence, severity within the combined category, or whether an event was judged related to treatment. Those details are not reported as part of this primary outcome definition.

The primary outcome population excludes 9 participants who were ineligible or did not receive treatment. The posted counts are 89 of 96 in the IMC-A12 group and 61 of 70 in the temozolomide group. These are descriptive counts from the registry record. A comparison between groups should be interpreted alongside its uncertainty, the population definition, and the limitations of the recorded safety information.

7. Results Posted in the Registry

• Temozolomide: 87.1% (61/70) versus 92.7% (89/96) on control; risk difference -5.6 percentage points (95% CI -15.0 to 3.8), risk ratio 0.94 (0.85–1.05); unadjusted two-proportion z-test p = 0.230.

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.

Response Rate (CR + PR)

• 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:
  • Temozolomide: 1.5% (1/65) versus 1.1% (1/90) on control; risk difference 0.4 percentage points (95% CI -3.3 to 4.1), risk ratio 1.38 (0.09–21.73); unadjusted two-proportion z-test p = 0.816.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Temozolomide and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome is response rate (CR + PR). It concerns tumor response during the period from treatment start through a maximum of 2 cycles, with each cycle described as 21 days, provided disease progression or unacceptable toxicity had not occurred. This outcome complements the primary safety endpoint by addressing a different dimension of treatment experience. It does not replace the primary result or alter what the adverse-event comparison measures.

The registry record lists a response estimate for each group and a comparison, but it reports no secondary analyses. The estimates should therefore be read as posted outcome data rather than as a fully documented confirmatory analysis. The absence of a reported analysis does not mean that no analysis was performed; it means the registry record does not provide one.

In general, secondary outcomes can help describe patterns beyond the primary question, but their evidential weight depends on how they were selected and analyzed. If many outcomes are examined, unadjusted tests can produce apparently notable results by chance. A multiplicity strategy can address this issue, for example by controlling how error is handled across a family of tests, but no such strategy is reported in the registry record.

The secondary response result should consequently be considered alongside its uncertainty, the limited observation window, and the lack of a reported analysis plan. It should not be combined informally with the safety result to make a single efficacy-and-safety conclusion. The registry does not report a prespecified method for balancing the different outcome domains, nor does it state that response was a confirmatory endpoint.

More broadly, the pattern across outcomes is not enough on its own to establish a treatment effect. A safety count and a response proportion answer different questions, have different timeframes, and may have different analysis populations. Their interpretation depends on definitions, missing-data handling, and prespecified statistical methods, several of which are not reported in the registry record.

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

• Response Rate (CR + PR)

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary comparison uses a risk difference: the estimated risk of the event in one group minus the estimated risk in the reference group, following the registry analysis convention. Unlike a relative measure, a risk difference expresses the contrast on an absolute scale. A value of zero corresponds to equal estimated risks; a negative or positive value indicates the direction of the contrast according to the order of groups. The posted estimate is negative, but its confidence interval crosses zero.

What does the confidence interval tell us?

A confidence interval describes the uncertainty around an estimated effect under the statistical method used. It is not a range that guarantees where the true effect lies, and it is not a measure of the probability that the result is correct. In general, a wider interval indicates less precision, while an interval that includes the no-difference value indicates that the data do not clearly distinguish a difference from no difference at the chosen confidence level. For this primary comparison, the 95% interval includes zero.

The posted p-value for the primary unadjusted comparison is 0.23. In general, a p-value describes how compatible the observed data are with a specified no-difference model, given the assumptions of the test. It is not the probability that the no-difference model is true, and it does not measure clinical importance. The registry record does not identify a complete analysis plan or say whether this comparison was adjusted for other factors.

Why is the endpoint a participant count?

The primary outcome is recorded as the number of participants with an event, rather than the total number of events. This distinction matters when one participant can experience multiple adverse events: the participant count answers how many people were affected at least once, while an event count would answer how many events occurred. The posted endpoint definition uses grade 3 or higher events during therapy and includes grades 3, 4, and 5. It does not provide participant-level event histories or a breakdown of the primary count by grade.

The registry identifies 96 participants in the IMC-A12 primary outcome group and 70 in the temozolomide group. The corresponding event counts are 89 and 61. Those counts provide the basis for the comparison, but do not reveal event timing, recurrence, or causality. The registry’s exclusion of 9 ineligible participants or participants who did not receive treatment defines the stated outcome population. Further information about missing data and the analysis population is not reported in the registry record.

How should the risk ratio and odds ratio be understood?

Risk ratios compare the event risk between groups as a relative measure. Odds ratios compare event odds, which are not the same as risks. When events are common, an odds ratio can be farther from one than the corresponding risk ratio, so the two measures should not be treated as interchangeable. General interpretation of either relative measure also depends on the group order and the outcome coding. The primary result is most directly described using the posted risk difference, while the relative measures provide alternate scales for the same comparison.

For binary outcomes, a normal approximation is one general method that can be used to construct intervals or plan sample sizes. Such methods can be less reliable in some settings, particularly when data are sparse or assumptions are poorly met. The registry record does not identify the method used for the sponsor’s primary analysis, so no particular test or interval procedure should be attributed to it. The planning illustration explicitly states a normal approximation, but that is a planning assumption rather than a reported description of the original trial analysis.

Why can over-dispersion matter?

Over-dispersion is a general issue for outcomes modeled as counts: the observed variation can exceed what a simple model assumes. When that occurs, a model that ignores the extra variation may understate uncertainty. The primary outcome in this record is a binary participant count, not a repeated-event count model, and the record does not report an over-dispersion assessment. The concept is relevant to statistical practice generally, but it should not be presented as a problem demonstrated in this trial.

What do the response results add?

The secondary response outcome is also binary in form, with response defined as CR + PR. It has a stated observation window of up to 2 cycles of 21 days each, subject to progression or unacceptable toxicity. Its estimates and comparison address a different question from the safety endpoint. The registry lists no reported analyses for the secondary outcome, so the posted estimates should not be described as a complete sponsor-reported inferential analysis.

Unadjusted analyses are comparisons that have not been adjusted for other variables or for the fact that multiple outcomes may have been examined. General statistical practice treats multiple unadjusted secondary tests cautiously, because examining many outcomes can increase the chance of at least one apparently notable result. The registry record does not describe a multiplicity procedure or provide the full analysis plan. As a result, the role of secondary results in confirmatory inference is not established.

11. Confidence Intervals and Precision

The primary risk-difference estimate has a 95% confidence interval that extends from negative to positive values, so it includes zero. This means the posted data are compatible with no difference and with effects in either direction within the interval. The estimate is therefore not precise enough to establish a clear separation between the groups on the primary outcome. The unadjusted p-value of 0.23 is consistent with that uncertainty, but it should not be interpreted as proof of equal risks.

Precision depends on the amount of information in the data, including the number of participants and how frequently the outcome occurs. The primary outcome counts were 89 of 96 in the IMC-A12 group and 61 of 70 in the temozolomide group. These counts describe the observed analysis groups; they do not remove uncertainty about the underlying risks or about how results might differ in another study population.

The 95% confidence intervals posted for the secondary response outcome also convey uncertainty. The secondary comparison’s interval includes zero, and the registry record lists no reported analyses for that outcome. Its estimates should therefore be read as descriptive evidence with uncertainty, not as a decisive finding. The statistical meaning of a confidence interval is general: under the method’s assumptions, it reflects the range of effect values compatible with the data at the stated confidence level.

Interval width is especially important when interpreting a comparison with relatively limited information. An interval can include both a potentially meaningful benefit and a potentially meaningful harm, even when the point estimate lies on one side of zero. The registry does not report a threshold for clinical importance, so statistical uncertainty cannot be translated into a judgment about whether a particular difference would matter clinically.

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 sample-size planning illustrations give participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two groups, a normal approximation, and an effect to detect set at the stated fraction of the observed effect. The registry record does not report the assumptions used for the trial’s original design or its original sample-size justification.

In plain language, the 80% power column gives the planned number of participants in each arm under which the calculation would have an 80% chance of detecting the selected effect, if that effect were the true one and the planning assumptions held. The 90% power column applies the same idea with a higher target chance of detection. These are planning quantities, not guarantees about the result of a particular study.

The rows consider planning for 100%, 75%, and 50% of the observed effect. The entries rise as the effect being targeted becomes smaller: a smaller difference is harder to distinguish from random variation, so the calculation requires more participants per arm. For example, the primary comparison’s illustration gives 458 participants per arm for 80% power and 613 for 90% power when planning for 100% of the observed effect; planning for 50% gives 1,607 and 2,150, respectively.

These values are not observed power. They are hypothetical planning illustrations calculated from the observed effect under the stated assumptions. They do not show what the trial was originally designed to detect, and they do not establish that the observed effect is the true effect. The planning curve should be understood in the same way: as a display of the relationship between the assumed effect size and the participants required under those assumptions, rather than as a forecast of a future study’s outcome.

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 = 0.927; treatment proportion p₁ = 0.871; average p̄ = 0.899.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4257 = 0.8343.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4238 = 0.3567.
4. n = (0.8343 + 0.3567)² / (-0.0557)² = 457.9, rounded up to 458 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 <- 0.927083333333333                          # control proportion
p1 <- 0.871428571428571                          # 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(1055314)
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 = 458 (80% power), 613 (90% power)
 75% of observed effect: n per arm = 765 (80% power), 1,024 (90% power)
 50% of observed effect: n per arm = 1,607 (80% power), 2,150 (90% power)
power.prop.test: 457.9 
Simulated power at n = 458 per arm: 0.800 (20000 replicates)

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

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists one secondary outcome, response rate (CR + PR), but does not report a multiplicity adjustment or a broader statistical analysis plan. Multiplicity refers generally to the increased chance of a false-positive result when several outcomes, comparisons, subgroups, or analyses are tested. A prespecified strategy can define which outcome is primary and how evidence across additional tests will be interpreted. The record identifies a primary safety endpoint, but does not explain whether or how secondary testing was controlled.

The secondary outcome has no reported analyses in the record. That absence limits assessment of the inferential role of the posted response estimates. It is not possible to tell from the registry whether the analysis was planned as exploratory or confirmatory, whether alternative analyses were considered, or whether any adjustment was applied outside the posted record. Such details are not reported in the registry record.

The primary outcome description states that 9 participants who were ineligible or did not receive treatment were excluded. This defines an outcome population, but the registry does not report a complete participant flow or clarify how the exclusion related to randomization. It also does not describe whether any outcomes were missing among participants who received treatment, how missing observations were handled, or whether sensitivity analyses were performed.

Analysis populations matter because including all randomized participants, only treated participants, or another defined group can answer different questions. A treated-participant analysis describes outcomes among those who received treatment, while an intention-to-treat analysis generally retains participants in their randomized groups regardless of treatment received. The registry record does not identify the primary analysis as intention-to-treat or provide enough information to determine whether another formal population definition was used beyond the stated exclusions.

The record also does not report the randomization method, allocation concealment, handling of protocol deviations, adjustment for baseline characteristics, or interim analyses. These omissions do not establish that such procedures were absent; they mean the registry entry does not document them. Without that information, the reported comparisons should be read as registry results with limits on how fully their analysis can be audited.

15. 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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: death nos (42.9%), hyperglycemia (10.4%), alanine aminotransferase increased (9.4%), diarrhea (8.3%), platelet count decreased (8.3%).

The primary safety outcome counts participants with grade 3 or higher adverse events during therapy. Separately, the registry reports serious adverse-event counts: 79 of 96 in the cixutumumab group and 40 of 70 in the temozolomide group. It also reports other adverse-event counts of 85 of 96 and 63 of 70, respectively. These categories should not be conflated with the primary endpoint: the record does not state that the serious-event category is identical to the grade 3+ primary definition.

The listed serious-event terms include Death NOS at 42.9%, Hyperglycemia at 10.4%, Alanine aminotransferase increased at 9.4%, Diarrhea at 8.3%, Platelet count decreased at 8.3%, and Sepsis at 8.3%. The registry does not specify the denominator for these term percentages in the posted information, so they should not be treated as percentages of all enrolled participants or as comparative rates between groups. Deaths are not separately reported in the safety-group data.

These figures describe events recorded in the registry. They do not establish that an event was caused by treatment, nor do they provide event timing, recurrence, or participant-level details. The serious-event counts and listed terms add context to the safety profile, but the missing definitions and denominators limit direct comparisons.

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

The posted data describe a randomized comparison of two treatment groups receiving intensive combination chemotherapy and radiation therapy, with cixutumumab in one group and temozolomide in the other. The primary endpoint counts participants with grade 3 or higher adverse events during therapy. The recorded counts are high in both groups, and the comparative risk-difference interval crosses zero. The result therefore leaves substantial uncertainty about the size and direction of the underlying difference.

This finding does not establish that the groups have equal safety outcomes. A non-significant unadjusted comparison is not an equivalence result, particularly when the registry does not report an equivalence margin or a design intended to test equivalence. Nor does the posted comparison establish that one regimen is safer. The interval and p-value describe statistical uncertainty under the analysis used, not a clinical recommendation.

The endpoint combines grades 3, 4, and 5 and counts participants rather than all events. It cannot show how many events an individual experienced, distinguish the separate severity grades, or establish whether events were treatment-related. The serious-event listings provide additional context but lack enough information to attribute individual events or compare term-specific risks.

The secondary response outcome addresses a different question and has no reported analysis in the registry record. It should not be used to convert the primary safety result into an overall claim about benefit. The record does not report a formal benefit-risk analysis or a statistical plan integrating response and adverse events.

Interpretation is also limited by the pilot-study setting, outcome population exclusions, and missing details about missing data and analysis populations. These limitations do not invalidate the posted counts; they narrow the conclusions that can be drawn from them. The results are a description of the groups and outcomes recorded in this trial, not a prediction of what would occur in every patient or a substitute for an individualized clinical judgment.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized design and a statistical comparison answer related but distinct questions. The group counts describe what happened among participants included in the primary outcome population. The risk difference estimates a comparative contrast, while its confidence interval shows how uncertain that estimate remains. A point estimate alone would hide the fact that the interval includes no difference and values on either side.

The endpoint also demonstrates the importance of defining the unit of analysis. A count of participants with at least one grade 3+ event differs from a count of all adverse events. The posted primary measure is useful for describing how many people experienced a qualifying event, but it does not characterize repeated events or their distribution across severity grades. Clear outcome definitions are essential to making the numerical results interpretable.

The registry’s planning illustrations show how sample-size requirements depend on the effect a future study aims to detect. Smaller targeted effects require more participants under the stated assumptions. Those illustrations are separate from the trial’s original design assumptions, which are not reported, and they should not be mistaken for evidence that the observed effect is reliable.

Finally, the record highlights the value of reporting analysis populations, missing-data methods, multiplicity plans, and outcome-specific analysis details. Without them, readers can describe the posted results but have less information for assessing how the analyses were selected and how robust the inferences are. These are central issues in the statistical reading of clinical trial evidence.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record leaves several trial-specific details unclear. The first group’s treatment schedule is truncated, so the full regimen cannot be reconstructed from the entry. Although the study is identified as randomized and unmasked, the randomization method, allocation concealment, and any stratification factors are not reported. The primary analysis population excludes 9 ineligible participants or participants who did not receive treatment, but a full participant flow and the relation of those exclusions to randomization are not reported.

The record does not explain how missing outcome data were handled, whether all assigned participants were analyzed in their assigned groups, or whether sensitivity analyses were conducted. It also does not report the detailed statistical plan, interim analyses, original sample-size justification, or any prespecified clinical importance threshold. These omissions restrict assessment of the analysis choices and the intended interpretation of the study.

The primary outcome combines grades 3, 4, and 5, and the registry does not provide a grade-specific breakdown in the primary result. It records participants with an event rather than the number and timing of all events. The safety term percentages have no stated denominator in the posted information, while deaths are not separately reported in the safety-group data. These details limit interpretation of the safety listings.

The response outcome is secondary and has no reported analysis in the registry record. The entry does not describe a multiplicity strategy or state the confirmatory status of that outcome. The observation window is limited to a maximum of 2 cycles, and the record does not provide a broader response follow-up analysis. These limitations are specific to the posted trial information and should shape how the secondary findings are read.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Temozolomide, Cixutumumab, and Combination Chemotherapy in Treating Patients With Metastatic Rhabdomyosarcoma — NCT01055314.
• Registry record last updated 2017-08-29; status last verified 2017-07.
• Results first posted 2017-07-28.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01055314 is a completed randomized, unmasked, parallel-group phase 2 pilot study sponsored by the National Cancer Institute (NCI). It enrolled 175 participants and compared chemotherapy and radiation therapy with cixutumumab against chemotherapy and radiation therapy with temozolomide in patients described as having high-risk rhabdomyosarcoma.

The primary outcome was the number of participants with grade 3 or higher adverse events during therapy, up to 54 weeks. The recorded counts were 89 of 96 in the IMC-A12 group and 61 of 70 in the temozolomide group. The risk-difference confidence interval crossed zero, and the unadjusted p-value was 0.23. Response rate (CR + PR) was posted as a secondary outcome, but the record lists no reported analyses for it.

The registry does not report the original sample-size justification, detailed statistical plan, missing-data methods, or multiplicity approach. The posted results are therefore best interpreted with attention to their uncertainty and the limits of the recorded analysis details.