IRESSA™ (Gefitinib) With Cisplatin Plus Radiotherapy for the Treatment of Previously Untreated Unresected Late Stage III/IV Non-Metastatic Head and Neck Squamous Cell Carcinoma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for IRESSA™ (Gefitinib) With Cisplatin Plus Radiotherapy for the Treatment of Previously Untreated Unresected Late Stage III/IV Non-Metastatic Head and Neck Squamous Cell Carcinoma (NCT00229723), a randomized phase 2 study. The primary outcome is Local Disease Control Rate at 2 Years.

2. Clinical Question

The trial addressed both dose and timing. Some groups received gefitinib during cisplatin and radiotherapy and then placebo; others continued gefitinib as maintenance, or received placebo during initial treatment and gefitinib as maintenance. This design makes the clinical question broader than whether gefitinib was used at all: it also concerns when it was given and at which dose.

The registry describes a phase 2 randomized, double-blind, placebo-controlled, multicentre comparative study. Its stated primary purpose was to assess local disease control at 2 years. The posted results give counts for seven treatment groups, while the comparisons reported in the registry-derived results contrast six gefitinib schedules with placebo/placebo. The record does not report a separate estimate isolating the effects of dose, timing, or their interaction.

3. Trial Design

This was a randomized, double-blind, placebo-controlled, multicentre phase 2 study with a factorial model and quadruple masking recorded in the registry. Enrollment was 224, and the study status is completed. The registry identifies AstraZeneca as the sponsor. It does not describe the masking roles or give further details about the randomization procedure.

All seven treatment groups included cisplatin and radiotherapy. One group received placebo during initial treatment and placebo as maintenance. Three groups received gefitinib with initial treatment, at 250 mg or 500 mg, followed by placebo or continued gefitinib at the same dose. Two other groups received placebo with initial treatment and gefitinib maintenance at either dose. These schedules allow comparisons across combinations of concurrent and maintenance treatment, but the posted results do not provide a single factorial estimate for each component or their interaction.

The primary endpoint was the number of participants with local disease control at 2 years. Secondary outcomes listed in the record include local disease control at 1 year, complete response, tumour response, progression-free survival, overall survival, and safety and tolerability. Counts are posted for several response outcomes, but secondary outcome analyses are not reported in the registry record. Results for progression-free survival and overall survival are not reported in the registry record.

The registry record does not report the original sample-size justification, planned statistical analysis, analysis populations, handling of missing outcomes, or interim-analysis procedures. The study's own design assumptions are therefore not established by the posted information. The sample-size illustrations accompanying the results are based on observed effects and stated planning assumptions, rather than documentation of the trial's original design.

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.

Only the first 6 of 7 groups are shown.

Concomitant Phase

Reasons for not completing this period:

Maintenance Phase

Reasons for not completing this period:

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.

Only the first 6 of 8 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Local Disease Control Rate at 2 Years, measured over Assessed at 2 yrs. Tumour assessments (clinical & by CT/MRI) were carried out during screening & regularly throughout the study until disease progression (as defined by Response evaluation criteria in solid tumours (RECIST))..

The primary endpoint was local disease control at 2 years, recorded as a number of participants. The registry defines control as having no evidence of treatment failure at that assessment. Failure included objective disease progression, according to RECIST, within the original irradiated area at an isodose level between 20% and 95%, or death. Tumour assessments were conducted clinically and by CT or MRI during screening and regularly during the study until disease progression.

Local control is relevant to the treatment strategy because the study combined radiotherapy with cisplatin and evaluated gefitinib schedules around that treatment. The endpoint focuses on progression in the treated area rather than all forms of disease progression. It is therefore distinct from progression-free survival and overall survival, which are also listed as secondary outcomes but do not have results reported in the registry record.

A count is not, by itself, a comparison of treatment groups. It must be read alongside the number assessed in each group, and interpreted with uncertainty in mind. The registry-derived comparisons express the difference in the proportion with local disease control between each gefitinib schedule and placebo/placebo. The endpoint definition also matters: death counts as failure, so the measure reflects both local progression and death under the stated rule. The registry record does not report additional details about how incomplete assessments or participants without a 2-year assessment were handled.

7. Results Posted in the Registry

• 250mg/Placebo: 29.2% (7/24) versus 35.0% (21/60) on control; risk difference -5.8 percentage points (95% CI -27.7 to 16.0), risk ratio 0.83 (0.41–1.70); unadjusted two-proportion z-test p = 0.608.
• 500mg/Placebo: 48.4% (15/31) versus 35.0% (21/60) on control; risk difference 13.4 percentage points (95% CI -7.9 to 34.7), risk ratio 1.38 (0.84–2.28); unadjusted two-proportion z-test p = 0.216.
• 250mg/250mg: 22.6% (7/31) versus 35.0% (21/60) on control; risk difference -12.4 percentage points (95% CI -31.5 to 6.6), risk ratio 0.65 (0.31–1.35); unadjusted two-proportion z-test p = 0.224.
• 500mg/500mg: 29.2% (7/24) versus 35.0% (21/60) on control; risk difference -5.8 percentage points (95% CI -27.7 to 16.0), risk ratio 0.83 (0.41–1.70); unadjusted two-proportion z-test p = 0.608.

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.

Local Disease Control Rate at 1 Year

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • 250mg/Placebo: 33.3% (8/24) versus 45.0% (27/60) on control; risk difference -11.7 percentage points (95% CI -34.3 to 11.0), risk ratio 0.74 (0.39–1.39); unadjusted two-proportion z-test p = 0.327.
  • 500mg/Placebo: 51.6% (16/31) versus 45.0% (27/60) on control; risk difference 6.6 percentage points (95% CI -15.0 to 28.2), risk ratio 1.15 (0.74–1.78); unadjusted two-proportion z-test p = 0.549.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 250mg/Placebo and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 500mg/Placebo and the control. The interval gives the range of effects that remain compatible with the data.

Complete Response

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • 250mg/Placebo: 29.2% (7/24) versus 46.7% (28/60) on control; risk difference -17.5 percentage points (95% CI -39.6 to 4.6), risk ratio 0.62 (0.32–1.23); unadjusted two-proportion z-test p = 0.142.
  • 500mg/Placebo: 35.5% (11/31) versus 46.7% (28/60) on control; risk difference -11.2 percentage points (95% CI -32.2 to 9.9), risk ratio 0.76 (0.44–1.31); unadjusted two-proportion z-test p = 0.307.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 250mg/Placebo and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 500mg/Placebo and the control. The interval gives the range of effects that remain compatible with the data.

Tumour Response (Complete Response + Partial Response)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • 250mg/Placebo: 45.8% (11/24) versus 56.7% (34/60) on control; risk difference -10.8 percentage points (95% CI -34.4 to 12.7), risk ratio 0.81 (0.50–1.32); unadjusted two-proportion z-test p = 0.368.
  • 500mg/Placebo: 54.8% (17/31) versus 56.7% (34/60) on control; risk difference -1.8 percentage points (95% CI -23.4 to 19.7), risk ratio 0.97 (0.66–1.43); unadjusted two-proportion z-test p = 0.868.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 250mg/Placebo and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 500mg/Placebo and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide related but distinct views of tumour control and response. Local disease control at 1 year concerns control at an earlier assessment than the primary endpoint. Complete response and combined tumour response describe response categories rather than the primary endpoint's failure-based local-control definition. Progression-free survival, overall survival, and safety and tolerability address other aspects of outcome and are listed in the registry, but results for those outcomes are not reported in the registry record.

The posted response counts do not change the central interpretation of the primary result: the comparisons are uncertain, and no single endpoint should be treated as a substitute for the others. Outcomes can differ because they measure different events, are assessed at different times, or apply different definitions. A pattern across outcomes can provide context, but it does not automatically establish a consistent treatment effect.

The registry-derived secondary comparisons are unadjusted. When many outcomes and comparisons are examined, the chance of a seemingly notable result arising by chance can increase. Unadjusted secondary findings therefore carry less weight than a clearly prespecified, adequately reported primary analysis, particularly when the analysis plan and multiplicity approach are not reported. The registry record does not report secondary outcome analyses or state how these outcomes were prioritized.

Secondary results can still be useful descriptively, especially for identifying questions that might warrant further study. Their role is limited by incomplete analysis reporting and by the absence of documented methods for missing data, analysis populations, and multiplicity. They should be treated as supporting context rather than as independent confirmation of the primary result.

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

• Local Disease Control Rate at 1 Year
• Complete Response
• Tumour Response (Complete Response + Partial Response)
• Progression Free Survival
• Overall Survival
• Safety and Tolerability

9. Statistical Interpretation

10. Statistical Methods Explained

Statistical interpretation begins with the outcome definition and the comparison being made. Here, the primary outcome is a count of participants meeting the local-control definition at 2 years. For each schedule, the posted comparison is against placebo/placebo. A risk difference describes the difference between the two group proportions: zero represents no difference, a value below zero indicates a lower proportion in the schedule group, and a value above zero indicates a higher proportion. The units are proportions, not a count of additional participants.

What does a confidence interval add?

In general, a confidence interval describes the range of values reasonably compatible with the data under the method used. It conveys uncertainty around the point estimate; it is not a range containing a fixed percentage of individual participant outcomes, nor does it assign a probability that the true effect lies in the interval. For the primary comparisons in this trial, every posted interval includes zero. That indicates that the data do not clearly separate the estimated difference from no difference using these intervals. Their breadth also shows that the estimates are imprecise.

How should the p-values be read?

In general, a p-value measures how surprising data at least as inconsistent with a null hypothesis would be if that hypothesis and the model assumptions were true. It is not the probability that the null hypothesis is true, nor a measure of the size or clinical importance of an effect. The posted primary p-values are unadjusted. The registry record does not describe the analysis model or report a multiplicity adjustment, so these values should not be treated as definitive tests of a prespecified family of comparisons.

Why does the group size matter?

With fewer observations, each participant's outcome has greater influence on a group's estimated proportion. That typically increases uncertainty, particularly when event counts are limited. In this study the group sizes differ, and the smallest groups contribute less information than larger groups. Confidence intervals help make this uncertainty visible; a point estimate alone does not.

Each comparison shares the same placebo/placebo group. These estimates are therefore not independent of one another: they reuse information from the same comparator. This matters when interpreting a set of comparisons together and when considering multiple testing. The posted results do not provide an overall test or a model that combines the schedules.

What is not documented?

The registry record does not report the trial's statistical analysis plan, the analysis population for the primary outcome, the approach to missing outcome data, or whether adjustments were made for baseline characteristics. It also does not report whether the analysis was intention-to-treat or based on another population. The registry-derived estimates should not be mistaken for a full account of the study's original analysis. There are no reported analyses for the secondary outcomes in the registry record.

General statistical considerations also apply to a multi-arm design. Comparing each arm separately with a common control can be useful for describing schedules, but does not automatically identify the separate contribution of each treatment component. A factorial analysis can estimate component effects or interactions when it is planned and reported; such results are not reported in the registry record. The treatment groups also combine dose and schedule in different ways, so a direct interpretation of any one comparison as a pure dose effect would go beyond the posted information.

The binary outcome counts can be compared as proportions, but the registry record does not state the exact statistical method used for the posted estimates. No assumptions about covariate adjustment, stratification, or model selection should therefore be imposed on the results. In general, the validity of an interval or test depends on the method's assumptions and the way participants and outcomes were included. Those methodological details are not reported in the registry record.

Finally, the primary outcome uses a composite failure rule: local progression or death counts as failure. Composite definitions can combine events with different clinical meanings. In general, interpretation benefits from knowing the contribution of each component, but the registry record does not provide a component breakdown for this endpoint. The reported count therefore describes the defined local-control outcome as a whole, not the separate frequency of progression and death.

11. Confidence Intervals and Precision

Precision is about how tightly the data locate an estimated treatment difference. The primary comparisons have confidence intervals that extend to both sides of zero. Thus each estimate is compatible with a lower local-control proportion and with a higher one relative to placebo/placebo. This is not evidence that the schedules are the same; it indicates that the available data do not pin down the direction or size of the difference with confidence.

The intervals are broad in relation to the point estimates, reflecting substantial uncertainty. The result is especially difficult to interpret as a narrow estimate of a schedule's effect because the groups are small and differ in size. A point estimate can appear substantial while its interval still includes no difference and values in the opposite direction. The interval should therefore take priority over a simple ranking by point estimate.

In general, a confidence interval communicates both the estimated effect and its precision. It does not capture every source of uncertainty: for example, uncertainty from missing outcomes, outcome measurement, analysis choices, or limitations in the registry record may not be reflected. Since the analysis population and missing-data handling are not reported in the registry record, the intervals cannot resolve those questions.

These estimates are also one part of a set of comparisons sharing a control group. Their individual intervals describe uncertainty for each comparison, but do not address multiplicity across the set. Taken together, the intervals support a cautious reading: the posted primary results are too imprecise to establish a clear difference between any one gefitinib schedule and placebo/placebo, and they do not demonstrate equivalence.

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 illustrative sample sizes per arm for the binary outcomes, not total event counts. The assumptions stated for these illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The trial's own original sample-size assumptions are not reported in the registry record.

The 80% power column represents the number of participants per arm that a hypothetical study would need, under those assumptions, to have an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses a higher chance of detection and generally requires more participants per arm. These are planning probabilities under an assumed effect and statistical model; they are not probabilities that a study result will be significant after it is completed.

Rows for smaller fractions of the observed effect correspond to more modest differences to detect. Smaller effects are harder to distinguish from random variation, so the planning requirement rises as the target effect gets smaller. The observed effect itself can be unstable, especially when group counts are limited; using it as a planning basis does not guarantee that a future study will have the same effect.

The sample-size illustrations are not observed power. They do not describe the power achieved by this completed trial, and they are not evidence that any comparison was or was not adequately powered according to the original protocol. A curve can be read as a visual expression of the same general relationship between target effect and required sample size, rather than as additional evidence about treatment outcomes.

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 = 0.350; treatment proportion p₁ = 0.292; average p̄ = 0.321.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6602 = 1.2939.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6589 = 0.5545.
4. n = (1.2939 + 0.5545)² / (-0.0583)² = 1,004.0, rounded up to 1,005 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 <- 0.35                          # control proportion
p1 <- 0.291666666666667                          # 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(229723)
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 = 1,005 (80% power), 1,344 (90% power)
 75% of observed effect: n per arm = 1,807 (80% power), 2,419 (90% power)
 50% of observed effect: n per arm = 4,113 (80% power), 5,505 (90% power)
power.prop.test: 1004 
Simulated power at n = 1,005 per arm: 0.794 (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 primary outcome is compared across six gefitinib schedules against the same placebo/placebo group. The registry-derived p-values are unadjusted, and the registry record does not report a correction for multiple comparisons or a hierarchy governing which comparisons should be interpreted first. When multiple hypotheses are tested, the chance of at least one false-positive finding can rise. Shared use of the control group also means the comparisons are statistically related.

The registry record does not report a statistical analysis plan describing whether the comparisons were planned as confirmatory or exploratory, what model was intended, or how the factorial structure would be analyzed. Although the study is labelled factorial, separate effects of dose and timing, and any interaction between them, are not reported. Without those details, the posted pairwise results should not be read as a complete factorial analysis.

Missing-data methods are not reported in the registry record. The record does not explain how participants without a 2-year assessment, participants who withdrew, or incomplete imaging assessments were handled. It also does not identify the analysis population used for the primary endpoint. These omissions matter because the interpretation of a participant count depends on who was included and how missing outcome information was treated.

The endpoint definition includes death as treatment failure, but the record does not give a separate breakdown of local progression and death within the primary outcome. Nor does it report sensitivity analyses for alternative assumptions about missing outcomes. These limitations make it difficult to assess how robust the reported comparisons would be under different analytic choices.

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

The posted data describe the number of participants meeting the registry's local disease control definition at 2 years in each treatment group and compare each gefitinib schedule with placebo/placebo. The point estimates vary in direction, and every confidence interval includes no difference. The results therefore do not identify a clear difference between a specific schedule and the comparator, while remaining too imprecise to rule out potentially meaningful differences.

These findings do not show that all schedules are equivalent. Demonstrating equivalence or non-inferiority requires a defined margin and an analysis designed for that purpose; such information is not reported in the registry record. Likewise, a non-significant unadjusted p-value does not prove that there is no effect. It indicates that the observed data do not provide strong evidence against the null under the test used.

The results also do not isolate the effect of gefitinib dose, concurrent use, or maintenance use. The groups combine these factors in different ways, and no separate factorial estimates are reported. Nor can the primary endpoint alone establish effects on progression-free survival, overall survival, or safety. Those are distinct outcomes, and results for some are not reported in the registry record.

Counts of adverse events are listed by group, but denominators at risk are not reported alongside those counts in the registry record. The counts should not be converted into comparative risks or rates. The record also does not provide enough detail to assess event timing, severity definitions, or exposure time. Accordingly, the primary outcome and adverse-event counts should be read as registry descriptions, not as a complete benefit-risk assessment.

In general, a trial result is evidence about the participants, treatments, outcome definition, and analysis represented in the record. It does not alone determine what should be done in an individual case or establish an effect in populations not described. The registry record does not provide the detail needed for broader clinical recommendations.

16. Why This Trial Matters Statistically

Statistically, this study is useful for illustrating the challenges of a multi-arm, factorial treatment question. The seven schedules combine differences in dose and timing, while the posted primary comparisons use a shared placebo/placebo group. That structure can answer specific pairwise questions, but a full account of dose, timing, and interaction effects requires an analysis that is not reported in the registry record.

The primary endpoint also demonstrates why effect estimates and confidence intervals matter alongside p-values. The point estimates move in different directions and the intervals remain compatible with no difference and with effects in either direction. Reading only the direction of a point estimate, or treating a non-significant test as proof of no effect, would miss the central issue: the results are imprecise.

The study further highlights the importance of reporting analysis populations, missing-data methods, multiplicity handling, and the original sample-size rationale. Without those details, readers can describe the posted counts and comparisons but cannot fully judge how the original analysis was planned or how sensitive it might be to analytic decisions. The planning illustrations are informative as general design examples, but do not replace the trial's unreported design assumptions.

Finally, endpoint definitions shape the question a study answers. Local disease control includes both progression in the irradiated area and death, while other outcomes capture response, survival, or safety. Keeping those measures distinct helps prevent a narrow endpoint from being interpreted as a complete account of treatment outcomes.

17. 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 primary outcome is reported as participant counts, but the registry record does not describe the analysis population, the handling of missing assessments, or whether all randomized participants were included. The endpoint assessment involved clinical evaluation and CT or MRI, but details of assessment adjudication and blinding at outcome review are not reported in the registry record.

The posted group sizes are uneven, and the comparisons rely on one shared control group. The resulting estimates have wide confidence intervals, and the individual comparisons do not provide separate estimates for dose or treatment timing. Although the design is labelled factorial, component-effect and interaction analyses are not reported.

The primary outcome combines local progression and death. A breakdown of those components is not reported in the registry record. The record also does not provide results for progression-free survival or overall survival, or analyses for all listed secondary outcomes. This limits the ability to relate the local-control findings to broader disease outcomes.

Safety information is incomplete for comparative interpretation: group denominators at risk are not reported with adverse-event counts, and the registry record does not provide event timing or exposure-adjusted measures. The trial's own statistical plan, sample-size justification, multiplicity procedure, and interim-analysis details are also not reported. These limitations restrict evaluation of the design and analysis beyond the posted summaries.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: IRESSA™ (Gefitinib) With Cisplatin Plus Radiotherapy for the Treatment of Previously Untreated Unresected Late Stage III/IV Non-Metastatic Head and Neck Squamous Cell Carcinoma — NCT00229723.
• Registry record last updated 2009-08-04; status last verified 2009-06.
• Results first posted 2009-08-04.
• 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.

21. Record Summary

NCT00229723 is a completed, randomized, double-blind, placebo-controlled, multicentre phase 2 study sponsored by AstraZeneca. The registry records a factorial model, quadruple masking, and enrollment of 224. It evaluated gefitinib at 250 mg or 500 mg alongside cisplatin and radiotherapy, with placebo or gefitinib maintenance schedules.

The primary outcome was the number of participants with local disease control at 2 years. Six posted comparisons contrast different gefitinib schedules with placebo/placebo. All primary confidence intervals include zero, and the estimates remain imprecise. The registry record does not report the original statistical plan, analysis populations, missing-data methods, multiplicity adjustment, or original sample-size rationale. Several secondary outcomes are listed, but secondary analyses are not reported in the registry record.