Temozolomide & RT Followed by Dose Dense vs Temozolomide & Retinoic Acid in Pts w/Glioblastoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Temozolomide & RT Followed by Dose Dense vs Temozolomide & Retinoic Acid in Pts w/Glioblastoma (NCT00200161), a randomized phase 2 study. The primary outcome is 12 Month Overall Survival of Patients With Newly Diagnosed Glioblastoma Multiforme Treated With Concurrent Temozolomide and Radiotherapy Followed by Dose Dense or Metronomic Dosing of Temozolomide and Maintenance Cis-retinoic Acid..

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group phase II trial with no masking recorded. The registry lists Memorial Sloan Kettering Cancer Center as the sponsor and records the study as completed. Its recorded start date is 2005-08-09, and its primary completion date is 2017-05-04. The registry enrollment is 127.

The treatment sequence began with concurrent temozolomide and radiotherapy. Participants were then assigned to the metronomic therapy cohort or the dose-dense therapy cohort. The arm descriptions distinguish the cohorts by the post-radiation temozolomide schedule: low dose in the metronomic cohort and high dose in the dose-dense cohort. The official title also names maintenance cis-retinoic acid, but further details of its use and timing are not reported in the registry record.

The primary endpoint is 12-month overall survival in patients with newly diagnosed glioblastoma multiforme. The record describes the outcome as a percentage of participants and follow-up as until death or date of last follow-up, averaging 12 months. The posted arm sizes for this endpoint are 43 in the metronomic cohort and 42 in the dose-dense cohort. Those endpoint-specific sizes are not interchangeable with the overall registry enrollment.

The record lists progression-free survival at 6 months as a secondary outcome, alongside outcomes concerning MGMT methylation status and efficacy in other malignant glioma subtypes. Numerical results are posted for progression-free survival at 6 months; analyses for the other listed secondary outcomes are not reported in the registry record. The original sample-size justification, detailed allocation procedures, and the trial's prespecified statistical analysis plan 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: 85 participants had a Glioblastoma diagnosis. The remaining participants consist of an exploratory cohort of Grade 3 tumors.

Overall 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 12 Month Overall Survival of Patients With Newly Diagnosed Glioblastoma Multiforme Treated With Concurrent Temozolomide and Radiotherapy Followed by Dose Dense or Metronomic Dosing of Temozolomide and Maintenance Cis-retinoic Acid., measured over until death or date of last follow up, an average of 12 months.

Overall survival concerns whether participants are alive at the assessment time, rather than whether their tumor has progressed or whether they have experienced a particular symptom. The primary outcome is recorded as the percentage of participants alive at 12 months. The registry describes the observation period as continuing until death or the date of last follow-up, averaging 12 months.

Overall survival is used in clinical trials because it is a direct, patient-important outcome. It avoids relying on an intermediate measure of disease status as a substitute for survival. In general, however, an endpoint's interpretation depends on how follow-up, censoring, and the analysis population are defined. Those operational details and the exact analysis method for this endpoint are not reported in the registry record.

The posted endpoint values are 69% for the metronomic cohort and 80% for the dose-dense cohort. These are descriptive percentages in the registry record. They do not, by themselves, establish that the difference between groups is precise or attributable to the treatment schedule. The comparative estimate and its uncertainty must also be considered.

7. Results Posted in the Registry

• Dose-Dense Therapy Cohort: 81.0% (34/42) versus 69.8% (30/43) on control; risk difference 11.2 percentage points (95% CI -7.0 to 29.3), risk ratio 1.16 (0.91–1.48); unadjusted two-proportion z-test p = 0.232.

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.

Progression Free Survival at 6 Months

• 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:
  • Dose-Dense Therapy Cohort: 57.1% (24/42) versus 46.5% (20/43) on control; risk difference 10.6 percentage points (95% CI -10.5 to 31.8), risk ratio 1.23 (0.81–1.86); unadjusted two-proportion z-test p = 0.327.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Dose-Dense Therapy Cohort and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists three secondary outcomes: progression-free survival at 6 months, the prognostic impact of methylated MGMT status, and preliminary efficacy data and MGMT impact in other malignant glioma subtypes. Numerical comparative results are posted for progression-free survival at 6 months. Analyses for the other listed secondary outcomes are not reported in the registry record.

Across the posted primary and secondary comparisons, the numerical point estimates favor the dose-dense cohort, but both comparisons are uncertain and their risk-difference confidence intervals include no difference. This broad pattern is useful as context for the primary result, not as a separate demonstration of a treatment effect. The endpoints measure different outcomes and timeframes, and their estimates are not independent pieces of evidence simply because they are listed separately.

Secondary results generally carry less weight than a clearly prespecified primary analysis. They may be exploratory, may involve different participant subsets or definitions, and can be affected by the number of outcomes examined. When several comparisons are considered, the chance of obtaining a nominally notable result can increase unless a suitable multiplicity strategy is planned and applied. The registry record does not report a multiplicity adjustment or enough detail to establish how these secondary outcomes were intended to support the primary question.

The posted progression-free survival result therefore provides additional descriptive information, but it does not resolve the uncertainty in the overall-survival comparison. The listed MGMT-related objectives cannot be evaluated from numerical results in the registry record. Avoid treating the pattern of point estimates as proof of consistency across outcomes: the available secondary reporting is incomplete, and no reported analyses clarify subgroup definitions, adjustments, or missing data.

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

• Progression Free Survival at 6 Months
• Prognostic Impact of Methylated MGMT Status.
• To Collect Preliminary Data on the Efficacy of This Regimen and Impact of MGMT Status in Other Malignant Glioma Subtypes.

9. Statistical Interpretation

10. Statistical Methods Explained

The registry presents a binary outcome, expressed as the percentage of participants with the event of interest. For the primary endpoint, the event is being alive at the 12-month assessment. The displayed percentages describe each cohort separately, while the comparative analysis estimates the difference between the dose-dense cohort and the metronomic cohort. The sign of a risk difference depends on the subtraction order; the registry comparison is framed as dose-dense versus metronomic.

What does a risk difference describe?

A risk difference subtracts one group's event probability from the other group's event probability. It is an absolute contrast on the probability scale. It can be interpreted as the change in event frequency between groups, rather than as a proportional change. For the primary outcome, the posted point estimate is positive, so the observed contrast points toward a higher proportion alive in the dose-dense cohort. The confidence interval, however, includes zero. A value of zero on this scale represents no difference between groups, so the interval leaves that possibility open.

The comparison is unadjusted. In general, an unadjusted estimate compares the observed group outcomes without accounting for other participant characteristics. Random allocation can help balance characteristics across groups on average, but it does not guarantee balance in a trial, especially when the groups are relatively small. An adjusted analysis can sometimes account for specified prognostic factors, but the registry record does not report an adjusted result or the covariates that might have been used.

How should the p-value be understood?

A p-value describes how compatible the observed data are with a specified null model, under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The primary unadjusted p-value is 0.232. This does not provide strong evidence against no difference by customary significance-testing conventions, but it also does not show that the schedules are equivalent. A non-significant result can arise when an effect is absent or when the data are too imprecise to distinguish an effect from no effect.

The registry does not report the test specification, whether the analysis was prespecified, or whether adjustments were made for other analyses. The sample-size illustration lists a two-sided significance level of 0.05, but that is an assumption for the planning illustration, not a reported account of the original trial's statistical plan. The original design assumptions are not reported in the registry record.

What does the confidence interval add?

A confidence interval describes uncertainty around an estimate under the statistical model used. In general, an interval that includes the no-difference value indicates that the data are compatible with no group contrast as well as with contrasts in either direction. The primary risk-difference interval includes zero, and it is broad enough to leave considerable uncertainty about the size and direction of the underlying contrast. The interval should be read alongside the point estimate rather than as a separate test that supplies a definitive answer.

Confidence intervals are not guarantees that a fixed percentage of individual outcomes fall within the limits. Nor do they show the range of outcomes that future participants will experience. Their meaning depends on the analysis method and assumptions. The registry does not report whether the interval used a particular small-sample correction, adjustment, or other method. The displayed comparison should therefore be understood as the posted unadjusted summary, not as a reconstruction of an unreported model.

Why do analysis details matter?

Overall survival can be affected by incomplete follow-up, and a time-to-event analysis commonly uses information about when events occur and when observation ends. The registry describes the primary outcome as a percentage and gives an average follow-up timeframe, but it does not report the statistical method used to handle censoring or the exact survival-analysis population. The posted binary summary does not contain the timing information needed to reproduce a time-to-event analysis.

The record lists no reported analyses. It also does not report an intention-to-treat definition, a per-protocol population, missing-outcome handling, baseline adjustment, or a multiplicity procedure. These details matter because different choices can change the interpretation of an estimate and its uncertainty. Without them, the most defensible reading is limited to the posted group percentages and the unadjusted comparison, with the stated uncertainty and the record's missing methodological details kept in view.

11. Confidence Intervals and Precision

The primary comparison has a positive point estimate: the posted values are 69% for the metronomic cohort and 80% for the dose-dense cohort. The confidence interval for the risk difference crosses zero. In general, zero is the value representing no difference on the risk-difference scale. Because the interval includes zero, the data are compatible with no difference as well as with a contrast favoring either cohort.

The interval is broad, so the estimate is not precise enough to identify a narrow range of plausible group differences. This is important even though the point estimate favors the dose-dense cohort in the posted comparison. An estimate's direction and its precision answer different questions: the direction describes the observed contrast, while the interval indicates how uncertain that contrast is under the analysis.

The primary unadjusted p-value is 0.232. It is consistent with the interval's failure to exclude no difference, but a p-value and a confidence interval are not substitutes for one another. The interval communicates a range of estimates compatible with the data and model; the p-value summarizes compatibility with a particular null model. Neither establishes equivalence or proves that an effect is absent.

The secondary progression-free survival comparison is also imprecise: its risk-difference interval includes zero, and its unadjusted p-value is 0.327. No numerical confidence limits need to be inferred from the arm percentages; the interpretation rests on the posted interval and comparison. The registry record does not report adjusted intervals, survival curves, or additional analyses that might clarify precision under other methods.

12. Planning a Similar Trial: Sample Size

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

The sample-size estimates are planning illustrations, not a description of the trial's original design. For this binary endpoint, each estimate is the number of participants per arm. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect used for planning is a stated fraction of the effect observed in the posted comparison. The trial's own original design assumptions are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for 80% power under the listed planning assumptions and effect size. In plain terms, power is the probability that a planned study would meet its specified statistical criterion if the assumed effect were the true effect and the model assumptions held. The 90% power column gives the corresponding participants per arm for 90% power. A higher target power generally requires a larger planned sample under otherwise comparable assumptions.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller assumed effects require more participants per arm to detect, which is why the estimates increase as the planning effect becomes smaller. These figures are sensitive to the observed effect used as their starting point; an unstable estimate from a small study can make an illustration a poor guide to the effect expected in a future study.

These estimates are not observed power. They do not describe the probability that the completed trial detected an effect, and they do not establish that the original trial was designed to meet these targets. The record gives no sample-size justification or original power calculation. The estimates should be read as hypothetical planning scenarios under the stated assumptions, not as retrospective evidence about trial success.

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 = 0.698; treatment proportion p₁ = 0.810; average p̄ = 0.754.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6094 = 1.1944.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6043 = 0.5086.
4. n = (1.1944 + 0.5086)² / (0.1118)² = 231.8, rounded up to 232 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 <- 0.697674418604651                          # control proportion
p1 <- 0.80952380952381                          # 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(200161)
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 = 232 (80% power), 310 (90% power)
 75% of observed effect: n per arm = 429 (80% power), 574 (90% power)
 50% of observed effect: n per arm = 999 (80% power), 1,336 (90% power)
power.prop.test: 231.8 
Simulated power at n = 232 per arm: 0.797 (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

Multiplicity arises when a study examines more than one outcome, comparison, subgroup, or analysis. In general, the more statistical tests considered, the greater the opportunity for a seemingly notable result to occur by chance if no adjustment or prespecified testing hierarchy is used. This concern is relevant to a record listing several secondary outcomes alongside a primary endpoint. The registry record does not report a multiplicity strategy, an adjustment, or a hierarchy for interpreting the secondary outcomes.

The record lists no reported analyses. It therefore does not clarify which analyses were prespecified, whether the posted comparisons were the only analyses conducted, or whether results were selected for posting. The absence of reported analyses is not evidence that analyses were not performed; it means that their methods and results are not reported in the registry record.

Missing outcome data and analysis populations also affect interpretation. The registry gives endpoint-specific arm sizes, but it does not describe whether every randomized participant was included in the primary analysis, how participants with incomplete follow-up were handled, or whether the comparison followed an intention-to-treat principle. It does not report reasons for missing observations or sensitivity analyses. For an overall-survival endpoint, information about follow-up and censoring is particularly relevant, but those details are not reported in the registry record.

The record also does not describe allocation concealment, adherence to assigned schedules, treatment crossovers, or a per-protocol population. These omissions do not show that a particular bias occurred. They limit the ability to assess how the randomized comparison was implemented and how robust the posted estimate is to analysis choices. The primary estimate should consequently be read as the registry's unadjusted comparison, without assuming unreported methods for missingness, multiplicity, or population selection.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event entries list zero participants with serious adverse events in the metronomic cohort and zero in the dose-dense cohort. The registry also lists no top serious adverse-event terms. For other adverse events, the entries record 43 affected among 43 at risk in the metronomic cohort and 42 affected among 42 at risk in the dose-dense cohort. The death entries are zero in the metronomic cohort and one in the dose-dense cohort.

These are descriptive registry counts. The record does not provide event-level details for the other adverse events, their severity, timing, duration, or relationship to treatment. It also does not report a statistical comparison of safety outcomes. Zero recorded serious adverse events does not establish that no serious event could occur, and the counts alone do not establish comparative safety. Interpret them as the entries posted for the recorded groups, not as a complete account of the types or clinical context of adverse events.

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

The results show that the posted 12-month overall-survival percentage was higher in the dose-dense cohort than in the metronomic cohort. The unadjusted comparison points in the same direction, but its confidence interval includes no difference and its p-value is 0.232. The estimate is therefore uncertain: the data do not precisely determine the size or direction of the underlying group contrast.

This result does not establish that the schedules are equivalent. Demonstrating equivalence would require a suitable prespecified margin and analysis, neither of which is reported in the registry record. Nor does the result establish a definitive advantage for either schedule. The point estimate is a description of the trial sample, while the confidence interval and p-value indicate that the comparison remains inconclusive.

The trial's randomized phase II design makes the comparison informative, but the posted data do not answer every question about the treatment sequence. The registry does not report detailed dosing, adherence, missing-data handling, adjusted analyses, or the original sample-size rationale. Its primary outcome is framed around newly diagnosed glioblastoma, while the broader record also mentions other malignant gliomas. The primary result should not be generalized to those other subtypes without corresponding reported results.

Progression-free survival at 6 months is also posted, but it is a secondary endpoint and does not settle the uncertainty in overall survival. The registry's MGMT-related secondary objectives lack reported numerical analyses. No medical decision should be inferred from these summary statistics alone; they describe the posted trial results and their statistical precision, rather than providing individual treatment guidance.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison should be read through both its point estimate and its uncertainty. The dose-dense cohort has a higher posted primary endpoint percentage, yet the confidence interval includes no difference and the unadjusted p-value is 0.232. A directional point estimate is not the same as a precise or conclusive estimate.

The record also illustrates the distinction between outcomes and analyses. It names several secondary objectives, but numerical results are posted only for progression-free survival at 6 months, and the registry reports no analyses. A list of endpoints does not establish that each was analyzed or that its results were prespecified. Statistical interpretation depends on the methods and reporting as well as on the values themselves.

Finally, the planning illustration highlights how sample-size needs depend on the assumed effect. Scenarios based on smaller fractions of the observed effect require more participants per arm. Because the illustration starts from an observed effect and is not the original trial design, it should not be mistaken for evidence of observed power or a retrospective justification of the trial's size. Together, these points make this record useful for understanding uncertainty, planning assumptions, and the limits of registry-level reporting.

18. Limitations

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

The primary outcome is presented as a percentage at 12 months, but the registry does not report the survival-analysis method, censoring details, or a full account of follow-up. The timeframe is described as until death or last follow-up, averaging 12 months; the record does not specify how participants without a complete 12-month observation contributed to the posted percentage.

The arm descriptions summarize the post-radiation temozolomide schedules as low dose and high dose but do not give doses or schedule details. Although the official title names maintenance cis-retinoic acid, its role in the arm descriptions is not detailed. This limits the ability to reconstruct the treatment regimens from the registry record alone.

The record is broader than the primary endpoint population: it refers to newly diagnosed glioblastoma and other malignant gliomas, while the primary endpoint is framed around glioblastoma multiforme. Results for other subtypes and the listed MGMT-related objectives are not reported. The record does not provide baseline characteristics, allocation concealment, treatment adherence, participant flow, or analysis-population definitions. These omissions restrict assessment of balance, implementation, and generalizability, without demonstrating that a specific bias occurred.

Finally, the registry lists no reported analyses and does not give the original sample-size justification, analysis plan, missing-data approach, or multiplicity procedure. The posted unadjusted comparison is therefore not accompanied by enough detail to independently verify all analytic decisions or determine whether additional analyses would materially change the interpretation.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Temozolomide & RT Followed by Dose Dense vs Temozolomide & Retinoic Acid in Pts w/Glioblastoma — NCT00200161.
• Registry record last updated 2018-03-07; status last verified 2016-09.
• Results first posted 2018-03-07.
• 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

This completed, randomized, unmasked, parallel-group phase II trial compared metronomic with dose-dense temozolomide after concurrent temozolomide and radiotherapy in newly diagnosed glioblastoma and other malignant gliomas. The registry lists enrollment of 127 and Memorial Sloan Kettering Cancer Center as sponsor.

The primary endpoint was 12-month overall survival. The posted percentages were 69% in the metronomic cohort and 80% in the dose-dense cohort. The unadjusted comparison is uncertain: its confidence interval includes no difference, and the p-value is 0.232. Progression-free survival at 6 months is also reported as a secondary outcome, while numerical results for the other listed secondary objectives are not reported in the registry record.

The registry does not report the original sample-size justification, detailed statistical plan, missing-data methods, or multiplicity strategy. The posted results are best understood as an imprecise comparison rather than a definitive conclusion about the schedules.