Ruxolitinib in Combination With Pemetrexed/Cisplatin in Non Small Cell Lung Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ruxolitinib in Combination With Pemetrexed/Cisplatin in Non Small Cell Lung Cancer (NCT02119650), a randomized phase 2 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

The statistical question is whether the posted survival data distinguish the two treatment groups, and how precisely they estimate the difference. The reported median overall survival was 7.5 months in the ruxolitinib group and 5.9 months in the placebo group. The estimated hazard ratio was 0.877, with an 80% confidence interval from 0.509 to 1.51 and a reported p-value of 0.756.

Those figures are estimates from this study, not a guarantee of what would occur in other settings. The confidence interval includes values on either side of 1, so it does not isolate a clear direction for the relative death hazard. The registry record does not report results for the listed secondary outcomes, including progression-free survival, objective response rate, duration of response, or treatment-emergent adverse events as a secondary endpoint.

3. Trial Design

This was a randomized, double-blind, phase 2 study with a parallel-group design. It compared ruxolitinib plus pemetrexed/cisplatin against placebo plus pemetrexed/cisplatin in people with nonsquamous non-small cell lung cancer that was Stage IIIB, Stage IV, or recurrent. The official title and brief summary describe pemetrexed maintenance after the initial combination treatment.

The registry reports an enrollment of 76. The overall-survival analysis used the intent-to-treat population, defined in the record as participants randomized in the study. The posted arm counts were 39 for ruxolitinib plus pemetrexed/cisplatin and 37 for placebo plus pemetrexed/cisplatin. These are the counts reported for the endpoint analysis.

The study started on 2014-02-11, and its primary completion date was 2016-02-11. Its status is listed as terminated. The reason for termination is not reported in the registry record, so the status alone does not explain whether or how it affected the conduct or interpretation of the study.

Overall survival was followed from randomization until death from any cause. Participants without an observed death at the time of analysis were censored at the last date known to be alive. The stated timeframe was up to 16 months or the data cutoff on 11FEB2016. The registry identifies the comparison method as the log-rank test and reports a hazard ratio with an 80% confidence interval. It does not report further details about the randomization procedure, treatment schedules, or the original design assumptions.

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: The intent-to-treat (ITT) population consisted of participants that were randomized in the study.

5. Baseline Characteristics

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

Population: The intent-to-treat (ITT) population consisted of participants that were randomized in the study.

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival (OS), measured over Randomization until death due to any cause; up to 16 months or data cutoff 11FEB2016..

Overall survival measures the time from randomization until death from any cause. It is a time-to-event endpoint: the outcome is not only whether an event occurred, but also how long participants were followed before death or censoring. The registry defines censoring for participants whose death had not been observed at the analysis: their follow-up ended at the last date they were known to be alive.

The primary endpoint was summarized using the Kaplan-Meier method, which estimates survival over follow-up while accounting for censored observations. The registry reports median overall survival in months for each group. A median is the estimated time by which half of the group’s survival distribution has experienced the event; it is not the survival time of every participant.

Overall survival is used because it captures time until death from any cause rather than relying on a narrower disease or response measure. The registry compared the groups with a log-rank test and reported a hazard ratio. The hazard ratio summarizes the relative event rate over follow-up under the analysis, while the confidence interval conveys uncertainty around that estimate. Neither the median estimates nor the hazard ratio alone describes every feature of the survival curves.

The stated analysis timeframe was randomization until death due to any cause, up to 16 months or the data cutoff on 11FEB2016. The record does not provide further detail on follow-up beyond that description.

7. Results Posted in the Registry

• Double-Blind Treatment: Ruxolitinib + Pemetrexed/Cisplatin vs Double-Blind Treatment: Placebo Plus Pemetrexed/Cisplatin: hazard ratio 0.88 (95% CI 0.51–1.51), reported p = 0.756 (as reported in the registry).

8. Statistical Interpretation

9. Statistical Methods Explained

The registry describes a time-to-event analysis. In this type of analysis, participants may have different lengths of follow-up, and some may not have experienced the event before their observation ends. The record defines the event as death from any cause and says that participants without observed death were censored at the last date known to be alive.

How does Kaplan-Meier estimation work?

Kaplan-Meier estimation uses the observed event times and the information from participants who are still being followed at those times. Censoring does not count as a death; it indicates that the participant’s event time is not observed through the end of available follow-up. The estimated survival curve changes when deaths occur and remains informed by participants’ follow-up until they are censored or experience the event.

The median is read from the estimated survival distribution as the time corresponding to the midpoint of that distribution. The registry reports medians of 7.5 months and 5.9 months for the two groups. These summaries do not show the entire shape of the survival curves. Two curves can have similar medians but differ at other points in follow-up, or have different medians while still having substantial uncertainty.

What does the log-rank test compare?

The log-rank test compares event experience between groups across follow-up. It uses the pattern of observed events and the participants at risk over time, rather than comparing only the two reported medians. The registry identifies this as the method for the primary comparison. The reported p-value is 0.756.

As a general statistical explanation, a p-value describes how unusual data at least as incompatible with a specified null model would be if that model and the test assumptions held. It does not give the probability that the null hypothesis is true, nor does it measure the clinical importance of an estimate. Its interpretation should be considered alongside the hazard ratio, confidence interval, sample information, and follow-up.

How should the hazard ratio be read?

The posted hazard ratio is 0.877 for ruxolitinib plus pemetrexed/cisplatin relative to placebo plus pemetrexed/cisplatin. A hazard ratio compares the event hazards between groups over the analysis. A value of 1 represents equal hazards under this summary; values below or above 1 indicate different estimated directions. The estimate is not a ratio of median survival times and does not mean that every participant has the same relative change in risk.

The registry reports an 80% confidence interval from 0.509 to 1.51. A confidence interval is a range of estimates compatible with the data under the analysis procedure, with the stated coverage level in repeated use of that procedure. It communicates uncertainty around the estimate; it is not a range containing a known fixed effect with certainty. Here the range includes 1, and the estimate is consequently not precise enough to settle the direction of the relative hazard.

What does censoring require?

In general, standard survival methods rely on assumptions about censoring, including that the censoring process does not systematically conceal a different event experience in a way that distorts the comparison. The registry explains when participants were censored, but further details about censoring patterns or checks of assumptions are not reported in the registry record. This means a reader can describe the stated method without claiming that every assumption was assessed or satisfied.

The record identifies the primary population as intent-to-treat: all participants randomized in the study. This population preserves the randomized group assignment for analysis and is often used to estimate the effect of assignment to the study groups. The exact handling of any participants with missing outcome information, apart from the stated survival censoring rule, is not reported in the registry record.

More generally, a hazard ratio is most straightforward to interpret when the relative hazards are reasonably stable over follow-up. The record does not report a proportional-hazards assessment or another diagnostic for this assumption. That absence does not establish that the assumption failed; it limits what can be concluded about how the reported summary was checked.

10. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimate. The registry reports the hazard ratio as 0.877, with an 80% confidence interval from 0.509 to 1.51. The interval spans values below and above 1, so it allows both directions for the relative hazard. The point estimate alone gives a narrower impression than the full interval and should be read together with it.

The confidence interval is reported at the 80% level, not the more familiar 95% level sometimes seen in clinical reports. A confidence interval is constructed by a procedure that, under its assumptions, would cover the target value at its stated rate over repeated applications. It is not a probability statement about this particular interval after the data have been observed. The reported p-value is 0.756 and accompanies the log-rank comparison.

The median estimates have lower confidence limits of 5.7 months for ruxolitinib and 4.0 months for placebo. Their upper confidence limits are not reported in the registry record. As a result, the record does not show complete confidence intervals for those medians, and their precision cannot be assessed fully from the listed bounds alone.

The endpoint analysis includes 39 participants in the ruxolitinib arm and 37 in the placebo arm. The number of deaths contributing to the comparison is not reported in the endpoint result. In time-to-event analyses, precision depends on event information and follow-up as well as participant counts. The study’s stated analysis timeframe was up to 16 months or the data cutoff on 11FEB2016. These details frame the uncertainty but do not justify deriving unreported event counts or follow-up summaries.

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 sample-size table and curve are planning illustrations based on the observed hazard-ratio effect, not a reconstruction of the study’s original design. For time-to-event outcomes, the displayed figures are total events, not participants per arm. The table considers planning for 100%, 75%, and 50% of the observed effect. For example, planning for 75% of the observed effect lists 3,241 total events for 80% power and 4,338 total events for 90% power. The 100% row lists 1,823 and 2,440 total events; the 50% row lists 7,291 and 9,760 total events, respectively.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect. The 80% power column describes the total events the illustration calculates for a design with an 80% chance of detecting the specified effect under those assumptions, if that effect and assumptions were correct. The 90% column describes the corresponding event target for a design with a 90% chance.

Smaller effects are harder to distinguish from random variation and therefore require more event information in this illustration. These figures are not observed power: they do not describe the probability that this completed study found an effect. The original trial’s own sample-size justification and design assumptions are not reported in the registry record. The table is a hypothetical planning aid, not evidence that the trial should or could have enrolled a particular number of participants.

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 = 0.877, so ln(HR) = -0.1312.
2. d = 4 × (1.96 + 0.842)² / [ln(0.877)]² = 1,822.6, rounded up to 1,823 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 <- 0.877                              # 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(2119650)
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 = 1,823 (80% power), 2,440 (90% power)
 75% of observed effect: events = 3,241 (80% power), 4,338 (90% power)
 50% of observed effect: events = 7,291 (80% power), 9,760 (90% power)
Simulated power with 1,823 events: 0.798 (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 2,705 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 76 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 <- 5.9          # control-arm median, months (converted from the posted unit)
hr          <- 0.877          # 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: 1680         p (1-sided)   0.0001
  Events: 823        ~HR at bound   0.7720
    Month: 15    P(Cross) if HR=1   0.0001
              P(Cross) if HR=0.88   0.0338
    IA 2: 67%                   Z   2.5114
      N: 2682         p (1-sided)   0.0060
 Events: 1646        ~HR at bound   0.8835
    Month: 24    P(Cross) if HR=1   0.0060
              P(Cross) if HR=0.88   0.5603
        Final                   Z   1.9930
      N: 2706         p (1-sided)   0.0231
 Events: 2468        ~HR at bound   0.9229
    Month: 60    P(Cross) if HR=1   0.0250
              P(Cross) if HR=0.88   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 primary analysis reports a hazard ratio of 0.877, an 80% confidence interval from 0.509 to 1.51, and a log-rank p-value of 0.756. These are the sponsor’s reported analysis results in the registry record. For this time-to-event endpoint, the displayed interpretation uses the reported hazard ratio rather than an independent recalculation from summary statistics.

That distinction matters because medians and their confidence bounds do not contain all the event-time information used in a survival comparison. Reconstructing a hazard ratio from those summaries would require assumptions not reported. The posted analysis therefore takes precedence; the record indicates no discrepancy between a sponsor result and a recalculated result.

The sponsor’s own result still needs to be read with its interval and the analysis details. The interval includes 1 and the p-value is 0.756, so the point estimate does not by itself establish a clear group difference. The registry does not report additional model diagnostics or a separate adjusted estimate for this comparison. The sample-size illustration is not the sponsor’s original design calculation; it is a planning illustration based on the observed effect.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies overall survival as the primary outcome and lists four secondary outcomes: progression-free survival, objective response rate, duration of response, and participants with treatment-emergent adverse events. It reports five outcome measures in total, but this record does not provide results for the listed secondary outcomes. It also does not report a multiplicity adjustment or a testing hierarchy for the outcomes.

Multiplicity arises when several outcomes or statistical comparisons are considered. As a general statistical matter, conducting more tests can increase the chance of at least one apparently notable result by chance. A prespecified strategy may address that issue, but the registry record does not report whether the study had such a strategy. The absence of a reported plan should not be read as proof that no plan existed; it means the plan cannot be evaluated from this record.

The primary analysis population is the intent-to-treat population, defined as participants randomized in the study. The record does not describe additional analysis populations, such as a per-protocol group, or report how participants were classified for any such analyses. No missing-data strategy is reported for the primary endpoint beyond the stated rule that participants without an observed death were censored at their last date known to be alive.

For survival data, censoring is a standard way to retain partial follow-up when the event has not been observed. Its validity depends on assumptions about how and why follow-up ends. The registry gives the censoring definition but not the amount or pattern of censoring by group, sensitivity analyses, or checks of censoring assumptions. It also does not report details on the handling of missing covariates or other incomplete data.

The record does not describe interim analyses, stopping boundaries, or the original statistical analysis plan. The study status is terminated, but the reason and any relationship between that status and the analysis are not reported. These gaps limit assessment of the full analysis process; they do not, on their own, show that the reported result is biased.

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: pneumonia (8.1%), anemia (7.7%), dyspnoea (7.7%), constipation (5.4%), atrial fibrillation (5.4%).

The registry reports serious adverse events in 19 of 39 participants in the ruxolitinib plus pemetrexed/cisplatin group and 16 of 37 participants in the placebo plus pemetrexed/cisplatin group. It also reports other adverse events in 37 of 39 and 36 of 37 participants, respectively. These are participant counts, not counts of distinct event episodes, and the record does not provide a comparison test for them.

The listed serious adverse event terms include pneumonia at 8.1%, anemia at 7.7%, dyspnoea at 7.7%, constipation at 5.4%, atrial fibrillation at 5.4%, and chronic obstructive pulmonary disease at 5.4%. The registry record does not identify these term percentages by treatment group in the displayed summary, so they should not be assigned to one arm or used to infer a between-group difference.

Adverse-event figures describe events recorded in this study; they do not by themselves establish that a treatment caused an event. The record lists no death counts in the adverse-event summary. It also does not provide the event-term detail or comparative analysis needed to interpret the full safety profile. These counts should be read alongside the registry’s limited follow-up and the absence of posted results for the secondary treatment-emergent adverse-event outcome.

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

The study’s posted overall-survival analysis describes a randomized comparison of ruxolitinib plus pemetrexed/cisplatin with placebo plus pemetrexed/cisplatin in nonsquamous non-small cell lung cancer that was Stage IIIB, Stage IV, or recurrent. The estimated medians were 7.5 months and 5.9 months, and the reported hazard ratio was 0.877. The 80% confidence interval, from 0.509 to 1.51, includes 1; the log-rank p-value was 0.756.

These results do not precisely establish the direction or size of a relative survival difference. They also do not demonstrate that the treatments are equivalent. A point estimate below 1 is not sufficient to establish a treatment effect when the uncertainty interval includes values on both sides of 1. Conversely, the imprecise result does not prove that there is no difference. The appropriate reading is that the posted estimate is uncertain.

The result applies to the analyzed trial population and the follow-up described in the record: randomization until death from any cause, up to 16 months or the data cutoff on 11FEB2016. The primary analysis was intent-to-treat. The registry does not report the reason for termination, the number of deaths in the endpoint summary, or complete confidence intervals for the medians.

The record’s purpose statement refers to safety and effectiveness, but the primary result is overall survival. Although adverse-event counts and selected serious-event terms are posted, the secondary outcome results are not. The available summary therefore cannot answer every question about treatment response, progression, duration of response, or safety. It supports a statistical description of the posted survival estimate and its uncertainty, not a broad conclusion about clinical benefit or harm.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate and its uncertainty should be read together. The reported hazard ratio is 0.877, but the 80% confidence interval extends from 0.509 to 1.51. Since that interval includes 1, the estimate does not settle the direction of the relative hazard. Reading only the point estimate would overstate what the posted analysis can establish.

It also shows why survival results cannot be reduced to a comparison of medians. The registry used Kaplan-Meier estimation for the medians and a log-rank test for the group comparison. Those methods use event timing and censoring information across follow-up. The medians are useful summaries, but they do not replace the hazard ratio, interval, test result, or survival curves.

The planning illustration highlights the relationship between effect size and information. In its calculations, smaller effects require more total events to achieve the stated power targets. These hypothetical targets should not be mistaken for the study’s original sample-size plan or for observed power. The registry record does not report the original design justification.

Finally, the record distinguishes what is available from what is not. It defines the intent-to-treat population and censoring rule, but does not report the number of deaths, complete median intervals, multiplicity strategy, or secondary outcome results. Such gaps matter because statistical interpretation depends not only on the headline estimate but also on the analysis population, event information, uncertainty, and transparency of the analysis plan.

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 record leaves several trial-specific details unavailable. It lists the study status as terminated but does not report the reason. It also does not report the original sample-size justification, treatment schedules, or detailed randomization procedures. The official title and summary mention pemetrexed maintenance, while the arm descriptions name the double-blind combination treatment without further maintenance details.

For overall survival, the record gives lower confidence limits for the two medians but no upper limits. It does not report the number of deaths contributing to the analysis, group-specific censoring patterns, or a detailed account of follow-up. The timeframe is stated as up to 16 months or the data cutoff on 11FEB2016, but further follow-up summaries are not reported.

The registry reports the log-rank method and the hazard ratio, but does not provide a proportional-hazards assessment, other model diagnostics, or sensitivity analyses. It does not report an interim-analysis plan or stopping rules. These omissions limit independent appraisal of the analysis assumptions and conduct; they do not establish that a specific assumption was violated.

Results for the listed secondary outcomes are not reported in the registry record. The adverse-event summary gives counts for serious and other adverse events and lists selected serious-event terms, but does not supply a full comparative safety analysis or deaths in that summary. The record also does not report a multiplicity strategy, detailed missing-data handling beyond the survival censoring definition, or alternative analysis populations.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Ruxolitinib in Combination With Pemetrexed/Cisplatin in Non Small Cell Lung Cancer — NCT02119650.
• Registry record last updated 2018-02-13; status last verified 2018-01.
• Results first posted 2017-06-14.
• 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

This registry record describes a randomized, double-blind, phase 2, parallel-group study of ruxolitinib or placebo with pemetrexed/cisplatin for nonsquamous non-small cell lung cancer that was Stage IIIB, Stage IV, or recurrent. The official title and summary also describe pemetrexed maintenance. Enrollment was 76, and the study status is listed as terminated.

The primary outcome was overall survival, measured from randomization to death from any cause. The registry reports Kaplan-Meier medians of 7.5 months and 5.9 months, a hazard ratio of 0.877, an 80% confidence interval from 0.509 to 1.51, and a log-rank p-value of 0.756. The interval includes 1, so the estimated relative hazard remains uncertain.

The record lists four secondary outcomes but does not report their results. It provides adverse-event counts and selected serious-event terms. The termination reason and the original sample-size justification are not reported in the registry record.