Study of Pralatrexate vs. Erlotinib for Non-Small Cell Lung Cancer After at Least 1 Prior Platinum-based Treatment: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Pralatrexate vs. Erlotinib for Non-Small Cell Lung Cancer After at Least 1 Prior Platinum-based Treatment (NCT00606502), a randomized phase 2 study. The primary outcome is Overall Survival (OS) of Patients Receiving Pralatrexate vs. Erlotinib.

2. Clinical Question

The trial asked whether overall survival differed between these two treatment groups in a population with advanced non-small cell lung cancer after prior platinum-based treatment. The registry record describes the study as randomized and phase 2b. Its stated purpose also included assessing safety, while the posted primary endpoint is overall survival. Response rate, progression-free survival, and adverse events are listed as secondary outcomes.

The posted median overall survival was 6.7 months for pralatrexate and 7.0 months for erlotinib. The sponsor-reported hazard ratio for pralatrexate versus erlotinib was 0.84, with a 95% confidence interval from 0.61 to 1.14. These statistics describe the observed results and their uncertainty; they do not, by themselves, establish that one treatment is superior. A p-value for the hazard ratio is not reported in the registry record.

3. Trial Design

The registry record describes a randomized, phase 2b, multicenter, parallel-group study with no masking. It lists 201 participants as the enrollment. The trial concerned non-small cell lung cancer and focused on people with stage IIIB/IV disease after failure of at least one prior platinum-based treatment. The brief summary further describes participants as current or former cigarette smokers.

Participants were assigned to pralatrexate or erlotinib. The posted outcome groups contain 100 participants for pralatrexate and 101 for erlotinib. The pralatrexate arm description specifies intravenous push administration over 3–5 minutes into a patent intravenous line containing normal saline. The erlotinib description specifies a 150 mg tablet taken daily, one hour before or two hours after food, until protocol discontinuation criteria were met. The registry record does not give the pralatrexate dose or schedule in the arm description. Vitamin B12 and folic acid appear in the interventions list, but their role and allocation are not explained there.

The study is marked completed. Its primary endpoint was overall survival, assessed from randomization and monitored no less frequently than every 16 weeks for up to 2 years after randomization. The record defines overall survival as time from randomization until death due to any cause. Participants alive at the data cut-off were censored at their last contact date. Response rate, progression-free survival, and adverse events are also listed as secondary outcomes.

Details such as the original sample-size justification, specific randomization procedures, allocation concealment, stratification factors, and the planned analysis population are not reported in the registry record. The record also does not describe the masking of outcome assessors or other trial personnel beyond stating that masking was absent.

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.

Randomization

Reasons for not completing this period:

Treatment

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.

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival (OS) of Patients Receiving Pralatrexate vs. Erlotinib, measured over Assessed from date of randomization no less frequently than every 16 weeks for up to 2 years after randomization..

Overall survival measures the time from randomization until death from any cause. In this trial, participants who were alive at the data cut-off were censored at their last contact date. Censoring means that a participant contributes follow-up information until the last time their survival status was known, without being counted as having died at that point.

Overall survival is a time-to-event endpoint: it uses both whether an event occurred and how long participants were followed before the event or censoring. It is often used in clinical trials because death is a clearly defined event and the endpoint does not depend on a judgment about whether a tumor response meets a particular definition. That general rationale does not establish how the trial chose its endpoint; the endpoint-selection rationale is not reported in the registry record.

The posted primary results give median overall survival for each group and a hazard ratio comparing the groups. A median describes the time by which half of the group’s estimated survival experience has reached the event; it does not mean that every participant survived for that duration. The hazard ratio summarizes the relative event rate over follow-up under a time-to-event model. These summaries answer related but distinct questions, and neither supplies the full survival experience of each participant.

The registry record says that overall survival was assessed no less frequently than every 16 weeks for up to 2 years after randomization. It does not provide a more detailed account of follow-up completeness, the data cut-off date, or how deaths were ascertained.

7. Results Posted in the Registry

• Pralatrexate vs Erlotinib: hazard ratio 0.84 (95% CI 0.61–1.14) (as reported in the registry).

8. Statistical Interpretation

9. Statistical Methods Explained

Overall survival is a time-to-event outcome. Each participant’s follow-up begins at randomization and ends at death or, if alive at the data cut-off, at the last contact date recorded for that participant. The latter observation is censored: it contributes information up to the known contact time, while the time of any later death is unknown. This approach allows participants with different follow-up durations to contribute to the analysis without treating their last contact as a death.

What does the median describe?

The median is a summary of the estimated survival distribution. It identifies the time at which the estimated probability of remaining alive has reached one half. It is not an average survival time, and it does not describe the outcome of every participant. A median can be reported even when some participants have not died, provided the observed follow-up supports estimation of that point in the survival distribution. The registry record reports median overall survival of 6.7 months for pralatrexate and 7.0 months for erlotinib, each with a 95% confidence interval.

These group-specific medians do not directly estimate a treatment contrast. Subtracting the medians would produce a difference between two point estimates, but would not supply the uncertainty for that contrast or account for the timing of events across follow-up. No median-difference estimate is reported in the registry record.

How should a hazard ratio be read?

The posted comparison is a hazard ratio from a Cox proportional hazards analysis. In general, a hazard is the instantaneous event rate among participants who have not yet had the event. A hazard ratio compares those rates between groups over follow-up. The reported value of 0.84 is for pralatrexate versus erlotinib; as a point estimate, it is below 1. This does not translate directly into a fixed difference in survival time or an individual participant’s probability of survival.

The Cox model is commonly used for time-to-event comparisons because it incorporates event timing and censored follow-up. Its usual proportional hazards interpretation assumes that the relative hazards are adequately represented by a constant ratio over time. That is a general model concept, not evidence that the assumption was checked or met in this trial. Diagnostics, covariate adjustments, stratification, and other modeling details are not reported in the registry record.

The 95% confidence interval for the reported hazard ratio is 0.61 to 1.14. In general, a confidence interval gives a range of values that are reasonably compatible with the observed data under the model and procedure used. The interval includes 1, the value corresponding to equal hazards under this parameterization. Its breadth also signals that the estimate is not highly precise. The registry record does not report a p-value for the hazard ratio.

What do censoring and follow-up imply?

Censoring is valid for standard survival methods when the censoring process does not systematically conceal different event risks in a way that distorts the comparison, conditional on the analysis. This is a general statistical consideration. The registry record describes the censoring rule for participants alive at data cut-off, but does not report the amount or reasons for loss to follow-up, the completeness of vital-status ascertainment, or a sensitivity analysis for censoring.

The stated assessment schedule was no less frequently than every 16 weeks for up to 2 years after randomization. The record does not give individual follow-up times, the number of deaths, or the number censored in each group. Without those details, readers cannot independently inspect the event distribution or recreate the survival analysis from the registry summary.

What can the planning illustrations tell readers?

The sample-size planning illustrations are based on the observed effect and use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For this time-to-event outcome, the displayed planning quantities are total events, calculated using the Schoenfeld approach. The illustrations consider 100%, 75%, and 50% of the observed effect and give event totals for 80% and 90% power. These are planning scenarios, not a record of the study’s original design assumptions. The original sample-size justification and assumptions are not reported in the registry record.

In general, a higher target power requires more information to detect a specified effect, and a smaller effect requires more information than a larger effect under otherwise fixed assumptions. In time-to-event studies, information is closely tied to event accumulation, so the listed totals are events rather than participants per arm. These illustrations should not be interpreted as observed power or as a retrospective verdict on whether the trial was adequate.

The registry record identifies one posted primary outcome analysis and lists three secondary outcomes. It does not describe a multiplicity strategy, analysis populations, missing-data procedures beyond the survival censoring rule, or a complete statistical analysis plan. Those omissions limit how far readers can evaluate the analysis choices from the registry entry alone.

10. Confidence Intervals and Precision

The primary comparison is reported as a hazard ratio of 0.84 for pralatrexate versus erlotinib, with a 95% confidence interval from 0.61 to 1.14. The interval expresses uncertainty around the estimated relative hazard. Under the usual interpretation, values below 1 favor a lower hazard in the pralatrexate group, values above 1 favor a lower hazard in the erlotinib group, and 1 represents equal hazards. Because the interval crosses 1, the data summarized by this interval are compatible with estimates on either side of equal hazards.

The interval spans a meaningful range of possible relative hazard values, so the point estimate should not be read as a precise measure of the size or direction of a difference. No p-value is reported for the comparison. The registry record also does not provide the model details needed to assess whether the interval accounts for covariates or other design features.

The group-specific median estimates are 6.7 months for pralatrexate, with a 95% confidence interval from 5.3 to 9.0 months, and 7.0 months for erlotinib, with a 95% confidence interval from 3.9 to 7.9 months. Those are intervals for each group’s median, not for a between-group contrast. Their overlap does not constitute a formal test of a treatment difference, and the registry record does not report a confidence interval for the difference between medians.

Confidence intervals generally reflect sampling uncertainty under the statistical method used; they do not incorporate every possible source of uncertainty, such as outcome misclassification, departures from model assumptions, or limits in how well the trial population represents other settings. The posted intervals help convey precision, but they cannot resolve limitations that are not assessed or described in the registry record.

11. 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 for this time-to-event endpoint are total event counts, not participants per arm. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the event totals use the Schoenfeld approach. The effect considered is a stated fraction of the observed effect. These are planning assumptions for the illustrations, while the trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column represents the total number of events that the planning calculation estimates would be needed to detect the specified effect with an 80% chance of reaching the chosen statistical decision threshold, if the planning assumptions hold. The 90% power column expresses the corresponding target for a higher chance of detection under those assumptions. Neither column describes the trial’s achieved power or its observed result.

The scenarios consider 100%, 75%, and 50% of the observed effect. As the effect to detect becomes smaller, the planning requirement rises: a subtler difference is harder to distinguish from random variation and generally calls for more information. For time-to-event analysis, that information is represented by events, rather than simply by the number of participants enrolled. Enrollment of 201 does not by itself show whether any planned event target was reached, because the registry record does not give the primary endpoint’s event count.

The plotted planning relationship represents the same general pattern: greater information is needed for a smaller target effect, and the higher power target calls for more events than the lower target. These figures are an illustration based on the observed effect, not observed power.

12. 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

d is the total number of events needed (Schoenfeld's formula) with 1:1 allocation and proportional hazards.

Worked calculation for this trial

1. Hazard ratio HR = 0.840, so ln(HR) = -0.1744.
2. d = 4 × (1.96 + 0.842)² / [ln(0.840)]² = 1,032.8, rounded up to 1,033 events in total 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
hr <- 0.84                              # observed hazard ratio
events_needed <- function(power, frac = 1) ceiling(round(4 * (z_a + qnorm(power))^2 / log(hr^frac)^2, 6))   # Schoenfeld, 1:1 allocation
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: events = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(events_needed(0.80, f), big.mark = ","), format(events_needed(0.90, f), big.mark = ",")))

# Simulation: given d total events under proportional hazards, events in the treatment arm are Binomial(d, hr / (1 + hr)).
# The score (log-rank type) statistic is (D1 - d / 2) / sqrt(d / 4).
set.seed(606502)
d    <- events_needed(0.80)
reps <- 20000
D1 <- rbinom(reps, d, hr / (1 + hr))
z  <- (D1 - d / 2) / sqrt(d / 4)
cat(sprintf("Simulated power with %s events: %.3f (%d replicates)\n", format(d, big.mark = ","), mean(abs(z) > z_a), reps))

Output from running the code

100% of observed effect: events = 1,033 (80% power), 1,383 (90% power)
 75% of observed effect: events = 1,837 (80% power), 2,458 (90% power)
 50% of observed effect: events = 4,132 (80% power), 5,531 (90% power)
Simulated power with 1,033 events: 0.810 (20000 replicates)

The simulation uses the fact that, with d events in total and proportional hazards, the number of events in the treatment arm is binomial. It is an approximation that conditions on the total number of events, and it should land close to the target power.

13. Group-Sequential Design Analysis

Many time-to-event trials, especially in oncology, stop or report early when interim data are overwhelming, so a single fixed-sample number understates the real design problem. The calculation below is an illustrative group-sequential design built from this trial's posted control median and hazard ratio. The registry record does not state the planned number of looks or the spending function, so the design is a planning illustration, not a reconstruction of the protocol. Assumed: one-sided α = 0.025, 90% power, three equally spaced looks on information, Lan-DeMets O'Brien-Fleming spending, 24 months of accrual, 60 months in total and a 1% monthly dropout hazard.

Under these assumptions the design needs about 1,560 participants in total, with the boundaries below.

Fixed design versus group-sequential alternatives

Group-sequential designs cost a small increase in maximum sample size and events compared with the fixed design, in exchange for the chance to stop early for overwhelming efficacy. O'Brien-Fleming spending keeps early boundaries very conservative and the final boundary close to the fixed-design value, whereas Pocock spending spends more alpha early.

Sensitivity to a smaller true effect

Planning for exactly the observed effect is optimistic, because observed effects in published trials tend to be somewhat larger than the true effect. The table repeats the main design (three looks, O'Brien-Fleming spending, 90% power) for smaller true hazard ratios.

For context, this trial enrolled 201 participants.

Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993. Agreement between the two packages confirms the boundary calculation.

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 6.7          # control-arm median, months (converted from the posted unit)
hr          <- 0.84          # hazard ratio used for planning
lambdaC     <- log(2) / med_control
eta         <- 0.01               # dropout hazard per month (assumption)
acc_months  <- 24                 # accrual duration (assumption)
study_months<- 60                 # total study duration (assumption)

design <- function(k, sfu, beta, h = hr) gsSurv(k = k, test.type = 1, alpha = 0.025, beta = beta, sfu = sfu,
  lambdaC = lambdaC, hr = h, hr0 = 1, eta = eta, gamma = 1, R = acc_months, T = study_months, minfup = study_months - acc_months)

# Main design: 3 looks, Lan-DeMets O'Brien-Fleming spending, one-sided alpha 0.025, 90% power
x <- design(3, sfLDOF, 0.10)
cat(sprintf("N_TOTAL|%s\n", format(ceiling(sum(x$gamma * x$R)), big.mark = ",")))
for (i in 1:3) cat(sprintf("GS|%d|%.1f|%.0f|%.3f|%.5f|%.5f\n", i, x$T[i], x$n.I[i], x$upper$bound[i], pnorm(-x$upper$bound[i]), cumsum(x$upper$spend)[i]))
cat("\n"); print(gsBoundSummary(x))

# Comparison of designs
cmp <- list(list("Fixed design, one analysis", 1, sfLDOF), list("Two looks, O'Brien-Fleming", 2, sfLDOF),
            list("Three looks, O'Brien-Fleming", 3, sfLDOF), list("Three looks, Pocock", 3, sfLDPocock))
cat("\n")
for (b in c(0.20, 0.10)) for (d in cmp) {
  y <- design(d[[2]], d[[3]], b)
  cat(sprintf("DES|%s|%d|%.0f|%s|%.1f\n", d[[1]], round(100 * (1 - b)), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ","), tail(y$T, 1)))
}

# Sensitivity: what if the true effect is smaller than the observed one? (3 looks, O'Brien-Fleming, 90% power)
cat("\n")
for (fr in c(1, 0.75, 0.5)) {
  y <- design(3, sfLDOF, 0.10, exp(log(hr) * fr))
  cat(sprintf("SENS|%.2f|%.3f|%.0f|%s\n", fr, exp(log(hr) * fr), tail(y$n.I, 1), format(ceiling(sum(y$gamma * y$R)), big.mark = ",")))
}

# Independent cross-check of the boundaries with rpact
r <- getDesignGroupSequential(kMax = 3, alpha = 0.025, beta = 0.10, sided = 1, typeOfDesign = "asOF", informationRates = x$timing)
cat(sprintf("\nCross-check, upper boundaries: gsDesign %s | rpact %s\n", paste(round(x$upper$bound, 3), collapse = ", "), paste(round(r$criticalValues, 3), collapse = ", ")))

Method: LachinFoulkes 
     Analysis               Value Efficacy
    IA 1: 33%                   Z   3.7103
      N: 1016         p (1-sided)   0.0001
  Events: 466        ~HR at bound   0.7091
    Month: 16    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.84   0.0338
    IA 2: 67%                   Z   2.5114
      N: 1560         p (1-sided)   0.0060
  Events: 932        ~HR at bound   0.8483
    Month: 25    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.84   0.5603
        Final                   Z   1.9930
      N: 1560         p (1-sided)   0.0231
 Events: 1398        ~HR at bound   0.8989
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.84   0.9000



Cross-check, upper boundaries: gsDesign 3.71, 2.511, 1.993 | rpact 3.71, 2.511, 1.993

14. Analyses Reported by the Sponsor

The posted hazard ratio is the sponsor-reported Cox proportional hazards estimate: 0.84 for pralatrexate versus erlotinib, with a 95% confidence interval from 0.61 to 1.14. The registry record does not report a p-value for this comparison or specify further details of the model. The displayed estimate is therefore the sponsor’s reported analysis, not an independently reconstructed comparison from individual participant data.

No discrepancy is flagged between the posted sponsor result and any recalculation. For this time-to-event outcome, the statistical summary uses the sponsor-reported hazard ratio rather than creating a new estimate from the group medians. A median and a confidence interval for each group are not enough to reconstruct the Cox model result: the hazard ratio depends on event timing and censoring across participants, and potentially on analysis choices not fully described in the registry record.

The planning illustrations are separate from the sponsor’s reported treatment comparison. They are calculated from the observed effect under stated planning assumptions and should not be confused with the original trial design or an additional sponsor analysis. The original sample-size justification and detailed statistical analysis plan are not reported in the registry record.

Accordingly, interpretation should keep the sponsor’s reported estimate, its confidence interval, and the missing analysis details distinct. The interval includes 1 and expresses uncertainty around the estimate; the registry record does not provide a reported p-value that would add another inferential summary.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists overall survival as the primary outcome and response rate, progression-free survival, and adverse events as secondary outcomes. It reports one primary analysis, but does not describe whether or how the analysis controlled for the possibility of false-positive findings across multiple outcomes, time points, or comparisons. A multiplicity strategy is not reported in the registry record.

Multiplicity is a general statistical concern when several hypotheses are tested: the chance of at least one apparently unusual result can increase as the number of tests grows, unless the analysis plan addresses that issue. This does not show that the trial’s results are invalid. It means the registry entry does not let readers determine whether a prespecified adjustment or testing hierarchy was used, particularly for secondary outcomes.

The record defines the primary endpoint and states that participants alive at data cut-off were censored at their last contact date. It does not describe other missing-data procedures, the extent of missing outcome information, loss to follow-up, or sensitivity analyses. For survival outcomes, censoring is part of the analysis rather than a complete solution to all missing-data concerns: the reasons for censoring and the relation between censoring and event risk can matter.

The planned analysis population is not reported in the registry record. It is therefore unclear from this entry whether the primary analysis used all randomized participants, a modified population, or another defined set. Details about protocol deviations, treatment discontinuation, adherence, and how these were handled are also not reported. No assumptions about intention-to-treat or per-protocol analysis should be inferred from the group counts alone.

Other details that would help assess the analysis—including covariate adjustment, stratification, proportional hazards diagnostics, interim analyses, and a complete statistical analysis plan—are not reported in the registry record. Their absence limits methodological review from this record, without establishing that the procedures were absent from the trial itself.

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: stomatitis (9.3%), dyspnoea (5.2%), respiratory failure (5.2%), thrombocytopenia (4.1%), pyrexia (4.0%).

The posted serious adverse event counts are 31 affected participants among 97 at risk in the pralatrexate group and 32 among 101 at risk in the erlotinib group. These are counts of participants with serious adverse events as listed in the registry record. They are not counts of all events, because a participant may experience more than one event; the record does not clarify event-level totals in this summary.

The record separately lists other adverse events affecting 91 participants among 97 at risk for pralatrexate and 94 among 101 at risk for erlotinib. These figures should be kept distinct from the serious adverse event counts. The registry also lists serious adverse event terms with percentages: stomatitis, 9.3%; dyspnoea, 5.2%; respiratory failure, 5.2%; thrombocytopenia, 4.1%; pyrexia, 4.0%; and dehydration, 4.0%. The entry does not specify group-specific denominators for these listed percentages in the summary.

The registry record does not report deaths in the safety summary, nor does this summary establish causation or allow a detailed comparison of event timing, duration, severity, or treatment relatedness. These figures describe the posted safety data; they are not a complete characterization of each participant’s experience.

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

The results describe a randomized comparison of pralatrexate and erlotinib for overall survival among people with advanced non-small cell lung cancer after prior platinum-based treatment. The posted median estimates are 6.7 months and 7.0 months, respectively. The sponsor-reported hazard ratio is 0.84, with a 95% confidence interval from 0.61 to 1.14. The interval includes 1, so the estimate does not pin down a clear relative direction of the hazard difference.

These statistics do not establish that either treatment is superior. They do not show that the treatments are equivalent, either: a confidence interval that includes equal hazards is not proof that the true difference is zero. The result is best described as an uncertain estimate, with the plausible values under the reported model extending to both sides of equal hazards. A p-value is not reported in the registry record.

The median values summarize estimated survival distributions but do not describe how every participant fared, the survival probability at a particular time, or the distribution of event times. The hazard ratio summarizes relative hazards over follow-up under a Cox model; it is not a direct measure of extra survival time. The registry entry does not provide the event counts, survival curves, model diagnostics, or details of any covariate adjustment needed for a fuller assessment.

The study population also matters to interpretation. The record concerns people with stage IIIB/IV non-small cell lung cancer, current or former cigarette smokers, and at least one prior platinum-based treatment. The result should not automatically be generalized beyond that population or setting. The registry record does not provide enough information to assess how participant characteristics or other treatments may have influenced outcomes.

Safety figures are descriptive counts and listed event percentages; they do not by themselves establish that an event was caused by a study treatment or provide a complete risk comparison. Overall, the posted data support a cautious account of observed estimates and uncertainty, rather than a claim that one treatment works better or that the two treatments have the same effect.

18. Why This Trial Matters Statistically

This trial illustrates why a time-to-event result should not be reduced to a single point estimate. The hazard ratio of 0.84 is the central estimate, but its 95% confidence interval from 0.61 to 1.14 conveys substantial uncertainty around that estimate and includes equal hazards. Reporting both the estimate and its interval prevents the point estimate from being mistaken for a precise or definitive treatment contrast.

The endpoint summaries also answer different questions. Median overall survival describes a point in each group’s estimated survival distribution, while the Cox hazard ratio compares event hazards across follow-up. The posted medians, 6.7 months for pralatrexate and 7.0 months for erlotinib, cannot substitute for the hazard ratio or establish a difference between the groups. The registry entry does not provide a direct median contrast with its uncertainty.

The trial is also a useful example of how planning calculations differ from trial results. The event totals in the planning illustrations depend on a specified effect and assumptions about significance level, allocation, and approximation. They do not reveal the trial’s original design rationale or its achieved power. Without the observed event count and the original sample-size justification, those planning values cannot establish whether the planned information target was met.

Finally, registry reporting is an important part of statistical interpretation. The entry gives the primary endpoint definition and sponsor-reported estimate, but does not report a p-value, multiplicity strategy, analysis population, or detailed model diagnostics. Identifying those gaps helps distinguish what the posted results support from questions that remain unanswered, without assuming that unreported procedures were not performed.

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 registry entry provides a limited account of the primary analysis. It reports a Cox proportional hazards estimate and confidence interval but does not describe model covariates, stratification, diagnostics, or whether the proportional hazards assumption was assessed. The p-value for the comparison is not reported. These omissions restrict independent evaluation of the analysis and its assumptions.

Detailed time-to-event information is also not included in the primary summary. The record does not give the number of deaths, group-specific censoring counts, individual follow-up distributions, or the survival estimates at specific time points. It describes censoring at last contact for participants alive at data cut-off, but does not report completeness of follow-up or reasons for missing contact information.

The entry does not report the original sample-size justification, interim analysis plans, a multiplicity strategy, or the defined analysis population. The planning illustrations are based on the observed effect and stated assumptions; they cannot recover the study’s original design rationale. Secondary outcomes are named, but their results and analysis details are not part of the primary outcome information summarized in the record.

Some intervention details are incomplete in the arm descriptions. The pralatrexate administration route is specified, but the dose and schedule are not described there. Vitamin B12 and folic acid are listed as interventions without an explanation of their role or allocation. The record also does not provide the detailed baseline characteristics needed to assess group comparability or the context of follow-up from this entry alone.

These are limitations of what the registry record reports. They should not be treated as evidence that the trial did not use procedures or collect information beyond what is included in the record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Pralatrexate vs. Erlotinib for Non-Small Cell Lung Cancer After at Least 1 Prior Platinum-based Treatment — NCT00606502.
• Registry record last updated 2021-03-05; status last verified 2021-02.
• Results first posted 2011-01-20.
• 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

The registry record describes a completed, randomized, unmasked, parallel-group phase 2b study of pralatrexate versus erlotinib in non-small cell lung cancer after at least one prior platinum-based treatment. Enrollment was 201. The primary outcome was overall survival, defined as time from randomization until death from any cause, with participants alive at data cut-off censored at last contact.

Median overall survival was 6.7 months for pralatrexate and 7.0 months for erlotinib. The sponsor-reported Cox hazard ratio for pralatrexate versus erlotinib was 0.84, with a 95% confidence interval from 0.61 to 1.14. A p-value is not reported in the registry record. The interval includes 1, leaving uncertainty about the relative hazard direction.

The record lists response rate, progression-free survival, and adverse events as secondary outcomes. It also reports serious adverse event counts and selected serious adverse event terms. Original sample-size justification, detailed analysis methods, multiplicity procedures, and analysis populations are not reported in the registry record.