Lapatinib Versus Placebo Given Concurrently With Cisplatin And Radiotherapy In Patients With Unresected Head And Neck Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Lapatinib Versus Placebo Given Concurrently With Cisplatin And Radiotherapy In Patients With Unresected Head And Neck Cancer (NCT00387127), a randomized phase 2 study. The primary outcome is Number of Participants (Par.) With Complete Response (CR), as Assessed by Independent Radiological Review.

2. Clinical Question

This is a comparison of treatment strategies across both the concurrent chemoradiation period and the follow-on monotherapy period. The study therefore does not isolate the contribution of lapatinib during chemoradiation from its contribution during the subsequent period. The posted primary endpoint concerns complete response at a specified assessment time, rather than a time-to-event outcome. The endpoint description says that assessments were based on Week 24 scans from participants receiving study treatment at that time and those in follow-up. The registry record gives a median assessment time of 13 months for the primary outcome.

3. Trial Design

The study was randomized, double-blind, placebo-controlled, multicentre, parallel-group, and phase II. It enrolled 67 participants and is recorded as completed. The registry lists the study start as 2006-11 and primary completion as 2009-06. The participants had unresected head and neck cancer, with the official title specifying stage III, IVA, or B squamous cell carcinoma.

Participants were assigned to chemoradiotherapy with placebo followed by placebo, or chemoradiotherapy with lapatinib followed by lapatinib. The lapatinib arm description gives a daily oral dose of 1500mg. The study summary describes one year of monotherapy after concurrent treatment. Cisplatin and radiotherapy were common components of both groups, so the intended contrast was the addition of lapatinib rather than a comparison of chemoradiation with no active treatment.

The posted primary analysis includes 33 participants in the placebo group and 34 in the lapatinib group. The primary outcome was the number of participants with complete response, assessed by independent radiological review at 6 months after chemoradiation. The registry specifies an Intent-to-Treat population for this endpoint, defined to include everyone randomized regardless of whether study medication was received.

The registry also lists investigator-assessed complete response, progression-free survival, overall survival, disease-specific survival, recurrence, and control outcomes among the secondary measures. Sixteen secondary outcomes have posted results. The registry record does not report the method used to generate the random sequence, details of allocation concealment, which parties were masked, or the protocol’s full operational schedule beyond the descriptions of treatment and outcome timing.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat (ITT) Population: all participants who were randomized to study treatment, regardless of whether they actually received study medication

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 Number of Participants (Par.) With Complete Response (CR), as Assessed by Independent Radiological Review, measured over From the date of randomization until 6 months post chemoradiation treatment, assessed for a median time of 13 months.

The primary endpoint counts participants who achieved complete response at 6 months after completion of chemoradiation. Independent radiological review assessed response using modified RECIST criteria. Under the definition in the registry record, complete response means disappearance of all target and non-target lesions. This endpoint turns scan assessments into a binary outcome for each participant: complete response or not complete response.

Complete response is used to describe tumor status at a prespecified assessment after chemoradiation. It gives a direct measure of the proportion meeting the registry’s radiological response definition at that time. Independent review is intended to separate endpoint assessment from the study treatment teams’ own judgments; the registry does not report further details about reviewer procedures or disagreements.

The endpoint is not the same as survival, durable disease control, or freedom from recurrence. A participant may meet the complete-response definition at the assessment without that result alone establishing what happens later. The registry separately lists outcomes such as progression-free survival, overall survival, recurrence, and loco-regional control. Those outcomes address different aspects of the disease course and have their own follow-up definitions.

The primary outcome description says the assessment was based on Week 24 scans from participants receiving study treatment at that time and participants in follow-up. The record identifies the analysis population as all randomized participants, but the handling of unavailable scans or other missing endpoint assessments is not reported in the registry record.

7. Results Posted in the Registry

• Chemoradiotherapy + Lapatinib, Followed by Lapatinib: 52.9% (18/34) versus 36.4% (12/33) on control; risk difference 16.6 percentage points (95% CI -6.9 to 40.0), risk ratio 1.46 (0.84–2.53); unadjusted two-proportion z-test p = 0.172.

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.

Number of Participants With CR, as Assessed by the Investigator

• 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:
  • Chemoradiotherapy + Lapatinib, Followed by Lapatinib: 50.0% (17/34) versus 21.2% (7/33) on control; risk difference 28.8 percentage points (95% CI 6.9 to 50.6), risk ratio 2.36 (1.13–4.93); unadjusted two-proportion z-test p = 0.014.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Chemoradiotherapy + Lapatinib, Followed by Lapatinib than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants Who Died Due to Progressive Disease

• 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:
  • Chemoradiotherapy + Lapatinib, Followed by Lapatinib: 23.5% (8/34) versus 33.3% (11/33) on control; risk difference -9.8 percentage points (95% CI -31.3 to 11.7), risk ratio 0.71 (0.33–1.53); unadjusted two-proportion z-test p = 0.373.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Chemoradiotherapy + Lapatinib, Followed by Lapatinib and the control. The interval gives the range of effects that remain compatible with the data.

Number of Participants With Loco-regional Recurrence of Initial Disease

• 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:
  • Chemoradiotherapy + Lapatinib, Followed by Lapatinib: 11.8% (4/34) versus 21.2% (7/33) on control; risk difference -9.4 percentage points (95% CI -27.1 to 8.2), risk ratio 0.55 (0.18–1.72); unadjusted two-proportion z-test p = 0.297.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Chemoradiotherapy + Lapatinib, Followed by Lapatinib and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary outcomes, including investigator-assessed complete response, progression-free survival, overall survival, disease-specific survival, death due to progressive disease, loco-regional recurrence and control, and distant recurrence. Sixteen secondary outcomes have posted results. The pattern among the outcomes with detailed comparisons is not uniform: investigator-assessed complete response points in a more favorable direction for the lapatinib group, while the posted comparisons for progressive-disease deaths and loco-regional recurrence are less conclusive.

The investigator assessment is related to the primary endpoint because both concern complete response, but it is not the same endpoint: the primary result was assessed by independent radiological review. Differences between assessment methods can matter, and the secondary result should not be used to replace the primary analysis. The other outcomes address different clinical events and follow-up questions; they cannot be treated as interchangeable measures of the primary endpoint.

Secondary results are usually less decisive when many outcomes are examined. Each additional test creates another opportunity for a chance finding, and the registry record does not report a plan for adjusting for multiplicity or identifying which secondary outcomes were confirmatory. A nominally small p-value for a secondary measure therefore carries less weight without a stated analysis hierarchy or multiplicity strategy. This does not make the result meaningless; it means that it is better treated as supportive or exploratory unless the prespecified role and analysis are clear.

The record lists several survival and recurrence measures, but the available summaries do not give complete detailed comparisons for every listed outcome. Conclusions should be confined to outcomes with posted estimates and uncertainty, rather than extrapolated from the pattern of the few detailed results. Taken together, the secondary findings add context but do not resolve the uncertainty in the independent-review primary outcome.

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

• Number of Participants With CR, as Assessed by the Investigator
• Progression-Free Survival (PFS), as Assessed by the Investigator
• Overall Survival (OS)
• Number of Participants Who Died Due to Progressive Disease
• Disease-specific Survival
• Number of Participants With Loco-regional Recurrence of Initial Disease
• Loco-regional Control
• Number of Participants With Distant Recurrence of Initial Disease

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary: each participant either met the complete-response definition at the assessment or did not. For a binary outcome, a group proportion describes the fraction of participants with the event. The posted primary counts are 12 of 33 in the placebo group and 18 of 34 in the lapatinib group. The corresponding proportions, 0.364 and 0.529, are the basis for describing the outcome by group.

What does a risk difference describe?

A risk difference subtracts the proportion in the comparator group from the proportion in the intervention group. It is expressed on the same absolute scale as the outcome proportions. A value of zero represents no difference in proportions; a positive value means the outcome proportion is higher in the intervention group, and a negative value means it is lower. The simple unadjusted recalculation gives a risk difference of 0.166, with a confidence interval from -0.069 to 0.401. This is a recalculation from posted summary statistics, not a replacement for the sponsor’s primary analysis.

Why are there different estimates?

The registry reports a sponsor analysis using Fisher Exact and gives the difference in percentage of participants with complete response as 10.7, with a 95% confidence interval from -13.4 to 37.3 and p = 0.366. The separate recalculation uses the posted counts to form a simple unadjusted risk difference and its interval and test. They are not the same analysis output. The registry record does not explain the numerical difference between these results, so no cause should be inferred from the summary alone.

What does Fisher Exact do?

Fisher’s exact test evaluates evidence against a null hypothesis of no association between group assignment and a binary outcome, using the observed counts. It is an exact test for the table of counts. Its p-value is conditional on the test’s assumptions and does not express the probability that the null hypothesis is true. It also does not measure the size or clinical importance of a difference. The size and uncertainty are better conveyed by the estimated contrast and its confidence interval, read alongside the counts.

How should the confidence interval be read?

A confidence interval gives a range of values compatible with the data under the interval procedure and its assumptions. In repeated use of the same procedure, the stated coverage level describes how often the procedure would capture the target value. It is not a range containing a known fixed percentage of individual participant outcomes, and it does not assign a probability to the true value after these particular data have been observed. The sponsor reports a 95% confidence interval for its primary analysis; the recalculated interval is a distinct estimate based on the posted counts.

When an interval for a difference includes zero, the data are compatible with no difference as well as with values on either side of zero within the interval. This is a statement about uncertainty, not proof that the groups are the same. Conversely, a p-value below a conventional threshold does not by itself establish a large, reliable, or clinically important effect. Interpretation depends on the endpoint, the analysis plan, the precision, and the possibility of chance findings across multiple outcomes.

Why does analysis population matter?

The registry defines the primary analysis population as Intent-to-Treat, including all randomized participants regardless of whether they received study medication. This preserves the comparison based on random assignment, subject to how outcome data are handled. The endpoint description refers to Week 24 scans from participants receiving treatment at that time and those in follow-up. The record does not explain how missing scans, incomplete assessments, or other deviations were handled in the primary analysis. That missing information limits assessment of whether the posted counts fully represent all randomized participants under the stated population definition.

General statistical context: small groups tend to produce less precise estimates than larger groups when other factors are similar. Sparse binary outcomes can also make estimates sensitive to a small number of participants. These issues matter when reading the confidence intervals and p-values, but they do not justify changing the observed counts or selecting a different analysis after seeing the results.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is a difference of 10.7 percentage points, with a 95% confidence interval from -13.4 to 37.3. This interval crosses zero. It is compatible with a lower complete-response percentage in the lapatinib group, no difference, or a higher percentage, across the values covered by the interval. Its breadth means the posted primary result does not pin down the magnitude of the between-group difference with much precision.

The simple unadjusted recalculation from the group counts gives a risk difference of 0.166, with an interval from -0.069 to 0.401. This interval also crosses zero. The recalculation and sponsor analysis should not be conflated: the sponsor reports Fisher Exact results, while the recalculation is a separate summary from the posted counts. The registry does not explain the difference between their point estimates and intervals.

General statistical context: confidence intervals reflect sampling uncertainty under the method used. An interval that includes the null value does not demonstrate equivalence, and an interval that excludes it does not measure the practical importance of the estimate. Precision is affected by the amount of information in the data, including the number of participants and the frequency of the outcome. Here the two randomized groups are small, and the interval remains compatible with materially different underlying response differences.

Precision also depends on the endpoint and analysis. The independent radiological review is primary; investigator-assessed complete response is a separate secondary measure. Their estimates and intervals should be interpreted as results for their own assessments rather than treated as interchangeable replications. The record’s missing-data procedures and multiplicity plan are not reported, which further limits a full appraisal of uncertainty and the strength of secondary findings.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on observed effects, not the original trial’s design calculation. For these binary outcomes, the figures are participants per arm. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row uses a stated fraction of the observed effect as the effect to detect. The trial’s own sample-size justification and original design assumptions are not reported in the registry record.

The 80% power column describes an illustrative group size per arm that, under the stated assumptions and effect, would give an 80% chance of rejecting the null hypothesis if that effect were the true effect. The 90% power column uses a higher target chance of detecting that effect under the same planning framework. These are prospective planning quantities, not measures of how likely the observed result is to be correct.

For the primary outcome, the planning illustration using 100% of the observed effect lists 140 participants per arm for 80% power and 187 participants per arm for 90% power. The rows using 75% and 50% of the observed effect show larger planning requirements. Smaller effects are harder to distinguish from random variation, so detecting them with the same power generally requires more participants.

These calculations are not observed power. Observed power calculated after a study is complete largely restates the observed estimate and does not resolve uncertainty. The illustrations also do not establish what the trial should have enrolled: the true effect may differ from the observed effect, and the registry record does not report the trial’s original sample-size assumptions. The figures should therefore be read as conditional planning scenarios, not as evidence about the trial’s success or adequacy.

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 = 0.364; treatment proportion p₁ = 0.529; average p̄ = 0.447.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.7031 = 1.3780.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6932 = 0.5834.
4. n = (1.3780 + 0.5834)² / (0.1658)² = 140.0, rounded up to 140 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 <- 0.363636363636364                          # control proportion
p1 <- 0.529411764705882                          # 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(387127)
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 = 140 (80% power), 187 (90% power)
 75% of observed effect: n per arm = 248 (80% power), 331 (90% power)
 50% of observed effect: n per arm = 550 (80% power), 736 (90% power)
power.prop.test: 140 
Simulated power at n = 140 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. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison as a Fisher Exact analysis of the difference in percentage of participants with complete response. The estimate is 10.7, the 95% confidence interval is -13.4 to 37.3, and p = 0.366. This is the sponsor-reported analysis to use when describing the registry’s primary result.

The simple recalculation from the posted group counts gives a risk difference of 0.166, a confidence interval from -0.069 to 0.401, and p = 0.172. It is explicitly an unadjusted recalculation from summary statistics, not the sponsor’s Fisher Exact output. It offers a transparent count-based comparison but should not be substituted for the sponsor-reported analysis or presented as though the sponsor reported those values.

The registry does not explain why the estimates differ. The record marks no discrepancy, but the distinct results should still be identified by their methods and source rather than blended into a single estimate. Both intervals include no difference, and each has substantial uncertainty. The sponsor’s result is the formal reported primary analysis; the recalculation is useful as a supplementary description of the posted counts, with its limitations kept clear.

15. Multiplicity, Missing Data and Analysis Populations

The registry record does not report whether the trial used a multiplicity adjustment, a hierarchical testing strategy, or another method for controlling the chance of false-positive findings across outcomes. It also does not identify a full confirmatory testing sequence. This matters because the registry lists many secondary outcomes and reports 18 outcome measures in total. When many hypotheses are tested, an isolated small p-value can occur by chance even if none of the underlying effects is present. Without the analysis plan, the strength of any secondary finding is difficult to calibrate.

The primary population is defined as Intent-to-Treat: all randomized participants, regardless of whether they received study medication. That definition supports interpretation according to randomized assignment. However, the endpoint description says that data are based on Week 24 scans from participants receiving study treatment at that time and participants in follow-up. The registry record does not report how missing scans, unevaluable scans, withdrawals, or other unavailable assessments were handled, or whether any imputation or sensitivity analysis was used.

The registry record does not report the original sample-size justification, the trial’s detailed statistical analysis plan, or whether interim analyses were conducted. It also does not report a missing-data plan or enough detail to assess the handling of protocol deviations. These omissions do not establish that such procedures were absent; they mean that their use and consequences cannot be assessed from the registry record.

The reported primary outcome is a count at a particular assessment time, while several secondary measures concern events over follow-up. The registry gives follow-up time descriptions for some outcomes, but not a complete account of censoring methods or analysis populations for every secondary measure. A clear distinction between fixed-time response and time-to-event outcomes is important: they answer different questions and depend on different analysis details. Those details are not all reported in the registry record.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anemia (9.7%), pneumonia (9.7%), dehydration (8.6%), mucosal inflammation (8.6%), diarrhea (8.6%).

The registry reports serious adverse events for 18 of 31 participants at risk in the chemoradiotherapy-plus-placebo group and 22 of 35 at risk in the chemoradiotherapy-plus-lapatinib group. The different at-risk counts should be retained when reading these figures; they are not the same as the randomized group sizes for the primary endpoint. The registry also reports other adverse events for 31 of 31 and 34 of 35 participants at risk, respectively.

The listed serious adverse event terms and percentages include anemia and pneumonia, each at 9.7%; dehydration, mucosal inflammation, and diarrhea, each at 8.6%; and dysphagia at 6.5%. These are registry-listed terms, not a complete account of each participant’s experience. The record does not report whether the events were judged related to study treatment, their severity beyond the serious-event classification, or the definitions and collection procedures needed for a full comparative safety analysis.

Deaths in the adverse-event summary are not reported in the registry record. The serious-event counts alone do not establish a causal relationship to treatment or provide a complete benefit-risk assessment. They describe reported events in the groups and should be interpreted with the differences in at-risk denominators and the limited detail available.

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

The primary result describes complete response at 6 months after chemoradiation, assessed by independent radiological review. The observed counts were 12 of 33 in the placebo group and 18 of 34 in the lapatinib group. The sponsor’s estimated difference was 10.7, with a 95% confidence interval from -13.4 to 37.3 and p = 0.366. The interval includes no difference and spans values in both directions, so the result is uncertain about the size and direction of the underlying difference.

This finding does not establish that the treatment groups were equivalent, nor does it establish a clear difference between them. A nonsignificant p-value is not proof of no effect. At the same time, the observed difference between the posted counts is not by itself proof of a true treatment effect. Estimates from a small study can be imprecise, and chance variation can produce apparent group differences.

The endpoint is a radiological assessment at a particular time. It does not alone establish longer-term survival, durable control, recurrence risk, or quality of life. The registry lists other outcomes relevant to those questions, but the posted primary result should not be expanded to answer them. Nor does the comparison separate the effect of lapatinib during chemoradiation from its effect during the follow-on monotherapy period, because the assigned strategies differed across both periods.

Secondary results add context but do not erase the uncertainty in the primary outcome. In particular, investigator-assessed complete response is a different assessment from independent radiological review, and the registry does not report a multiplicity plan for the many secondary outcomes. The results describe this trial and its recorded endpoints; they do not establish what would happen in other populations, under different treatment schedules, or in later practice.

General statistical context: a result should be read through its estimate, confidence interval, design, and analysis population, not through a p-value alone. The registry record leaves important details about missing data and the original statistical plan unreported, which limits how far the results can be interpreted beyond the reported comparisons.

18. Why This Trial Matters Statistically

This trial illustrates the distinction between an observed group difference and a precise estimate of an underlying effect. The lapatinib group had more participants recorded with complete response in the posted counts, but the sponsor’s primary confidence interval includes no difference and extends to values on either side. Statistical interpretation therefore requires both the direction of the point estimate and the uncertainty around it.

It also shows why analysis methods and assessment definitions matter. The sponsor reports a Fisher Exact analysis for the primary endpoint, while a separate simple recalculation from the counts gives another estimate. Both should be clearly labeled rather than merged. Independent radiological review and investigator assessment are also distinct measures, even though both concern complete response.

The treatment contrast includes lapatinib during concurrent chemoradiation and continued lapatinib afterward, compared with placebo across both periods. This design estimates the contrast between those full assigned strategies; it does not isolate the contribution of either treatment period. The distinction is important when interpreting what the randomized comparison can answer.

Finally, the registry lists numerous secondary outcomes, but does not report a multiplicity plan, the original sample-size justification, missing-data handling, or interim-analysis procedures. These omissions do not tell whether the methods were absent; they limit how fully the results can be appraised. The study is a useful example of how randomized design, outcome definition, reporting detail, and interval precision jointly shape the interpretation of a trial result.

19. Limitations

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

The primary comparison is based on 67 randomized participants, divided between groups of 33 and 34 for the posted endpoint. The confidence interval for the sponsor-reported primary estimate is broad and includes no difference, limiting precision. Small group counts also mean that a few participant outcomes can have a noticeable effect on the estimated proportions.

The registry record does not report the original sample-size justification, detailed statistical analysis plan, missing-data procedures, or whether interim analyses were conducted. Although the primary population is defined as Intent-to-Treat, the endpoint description refers to scans from participants receiving treatment at the assessment and those in follow-up. The record does not explain how unavailable or unevaluable scans were handled. These reporting gaps make it difficult to assess the robustness of the primary estimate to missing assessments or alternative analytic choices.

The primary endpoint is a fixed-time radiological response, not a direct measure of long-term survival or durable disease control. The trial’s two treatment strategies differ both during concurrent chemoradiation and during the subsequent monotherapy period, so the contribution of each period cannot be separated from this comparison. The trial is phase II, and its posted estimates should be interpreted in that setting rather than as definitive evidence about all relevant outcomes.

The registry provides detailed comparisons for only some secondary measures, and it does not report a multiplicity adjustment plan. Secondary findings may therefore be more vulnerable to chance findings across the outcome set. The serious adverse event summary includes at-risk denominators that differ from the primary randomized group sizes, while treatment attribution and other safety-analysis details are not reported. These limitations concern the information available in the registry record; they should not be read as proof that unreported procedures or analyses were not performed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Lapatinib Versus Placebo Given Concurrently With Cisplatin And Radiotherapy In Patients With Unresected Head And Neck Cancer — NCT00387127.
• Registry record last updated 2015-06-25; status last verified 2015-02.
• Results first posted 2015-01-05.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT00387127 is a completed randomized, double-blind, placebo-controlled phase II study in unresected head and neck squamous cell carcinoma. It enrolled 67 participants and compared lapatinib with placebo, each given with cisplatin and radiotherapy and followed by the corresponding monotherapy. The primary endpoint was complete response at 6 months after chemoradiation, assessed by independent radiological review.

The posted primary counts were 12 of 33 in the placebo group and 18 of 34 in the lapatinib group. The sponsor reported a difference of 10.7, a 95% confidence interval from -13.4 to 37.3, and p = 0.366. The interval includes no difference and is broad. A separate unadjusted recalculation from the counts gives a risk difference of 0.166, with an interval from -0.069 to 0.401 and p = 0.172; it is not the sponsor’s reported analysis.

The registry lists numerous secondary outcomes and serious adverse events. Important details, including the trial’s original sample-size justification, multiplicity plan, missing-data procedures, and interim-analysis procedures, are not reported in the registry record.