Study of TH-302 or Placebo in Combination With Pemetrexed in Patients With Non-squamous Non-small Cell Lung Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of TH-302 or Placebo in Combination With Pemetrexed in Patients With Non-squamous Non-small Cell Lung Cancer (NCT02093962), a randomized phase 2 study. The primary outcome is Overall Survival.

2. Clinical Question

The clinical question is comparative: the relevant contrast is between the two randomized treatment groups, not whether either group changed from its own starting point. Because pemetrexed appears in both regimens, the trial addresses the added contribution of TH-302 within that combination, rather than a comparison of pemetrexed with no pemetrexed. The registry record labels the study randomized, double-blind in its official title, and triple-masked in its design fields. The record does not specify which people were included in the masking designation.

3. Trial Design

This was a randomized, parallel-group phase 2 study with a planned enrollment of 265 participants. The official title describes it as double-blind, placebo-controlled, and multicenter; the registry design fields identify triple masking. The record does not give further details about the centers, allocation sequence, or masking procedures. The trial compared TH-302 plus pemetrexed with matching placebo plus pemetrexed, with 134 participants listed in the TH-302 group and 131 in the placebo group.

The registry gives a study start of 2014-06 and primary completion of 2016-04. Its current status is terminated. The record does not state why the trial was terminated, whether termination occurred before or after the planned enrollment was reached, or how termination affected follow-up. It lists an enrollment of 265, matching the total of the two posted arm counts, but those figures describe registry enrollment and group counts rather than a complete account of who was analyzed for each outcome.

The primary outcome is overall survival, with a 2 years timeframe. The posted outcome is represented as a count of participants in each arm: 51 in the TH-302 and pemetrexed group and 49 in the placebo and pemetrexed group. No outcome analyses are posted in the registry record, and no secondary outcomes are posted. Although the brief study description refers to safety and effectiveness, the trial record does not provide a detailed statistical plan or explain the analysis populations for the outcome counts.

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

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, measured over 2 years.

Overall survival is a time-to-event concept: in general, it measures the time from a defined starting point until death from any cause. It is commonly used in oncology trials because it captures a direct outcome important to patients and does not require deciding whether a particular cause of death was related to the cancer or treatment. That is a general explanation; the registry’s outcome description does not report the exact time origin, censoring rules, or event definition used in this trial.

The registry labels the primary outcome Overall Survival and gives a 2 years timeframe. However, its posted values are counts of participants: 51 in the TH-302 plus pemetrexed arm and 49 in the placebo plus pemetrexed arm. The record does not explain what event those counts represent or how they were derived from follow-up. It does not post time-to-event quantities such as a median, a hazard ratio, or a survival estimate at a specified time. Consequently, the counts alone do not describe how long participants lived or the timing of any events.

A complete interpretation of an overall-survival comparison normally depends on the analysis definition and the handling of participants whose event status is not observed during follow-up. Those details are not reported in the registry record. The available counts should therefore be read as the recorded outcome values, not as a substitute for a reported survival analysis.

7. Results Posted in the Registry

• TH-302 and Pemetrexed: 38.1% (51/134) versus 37.4% (49/131) on control; risk difference 0.7 percentage points (95% CI -11.0 to 12.3), risk ratio 1.02 (0.75–1.39); unadjusted two-proportion z-test p = 0.912.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a randomized comparison estimate?

In general, random allocation aims to distribute measured and unmeasured participant characteristics across treatment groups, so that the between-group contrast can be interpreted as a comparison of assigned regimens. This is a general statistical principle, not a claim that the groups were identical in this trial. The registry identifies the study as randomized and parallel-group but does not describe sequence generation, concealment, stratification, or the analysis population. The comparison reported is between TH-302 plus pemetrexed and placebo plus pemetrexed.

A treatment effect is ordinarily expressed through a contrast between groups, such as a difference in risks, a ratio of risks, or a time-to-event measure. The posted comparison uses a risk difference. General interpretation: a risk difference compares the proportion with an event in one group against the proportion in the other, on an absolute scale. The registry labels the outcome as a participant count and does not explain the event definition or the derivation of the reported risk difference. The posted estimate is close to zero, and its confidence interval crosses zero, so the comparison does not isolate a difference in either direction.

What does a confidence interval describe?

In general, a confidence interval expresses uncertainty around an estimate under a specified statistical model and sampling procedure. A wider interval means the data are consistent with a broader range of effect sizes; an interval crossing the no-difference value indicates that the data do not rule out no difference under that method. For the posted risk difference, zero is the no-difference value, and the interval extends to both sides of it. The registry does not provide an adjusted analysis or explain which interval method was used.

A confidence interval is not a guarantee that the true effect lies inside the interval, nor does it express the probability that the treatment effect has a particular value. It also cannot repair uncertainty about how the endpoint was defined or who was included. Here, those interpretive details are not reported in the registry record, and there is no posted time-to-event estimate to complement the count comparison.

How should the p-value be read?

The posted unadjusted p-value is 0.912. In general, a p-value measures how incompatible the observed data are with a specified null model, assuming that model and the test procedure are appropriate. It is not the probability that the null hypothesis is true, and it does not measure clinical importance. A large p-value can occur when groups are similar, when the data are imprecise, or both. It does not prove that two regimens are equivalent.

The record does not identify the test underlying this unadjusted p-value or state whether it was the planned primary analysis. It also does not report a multiplicity adjustment. The p-value should therefore be read as the posted unadjusted comparison, rather than as confirmation of a complete prespecified analysis. The statistical analysis plan and the original protocol assumptions are not reported in the registry record.

Why does time-to-event analysis require additional detail?

General survival analysis uses both event occurrence and the time at which an event occurs. Participants who have not had an observed event by the end of available follow-up can contribute partial information through censoring, provided the analysis rules and assumptions are appropriate. The timing and amount of follow-up, censoring definition, and method of analysis can affect interpretation. The registry gives a 2 years timeframe but does not report those details for this outcome.

Participant counts alone do not show whether an event occurred early or late, or whether some participants had shorter observation. For that reason, a count-based result is not interchangeable with a survival curve or a hazard ratio. The registry posts none of those time-to-event summaries, so they cannot be used to characterize the survival experience in this trial.

What is the role of the planning illustration?

The sample-size illustration uses the observed effect as its starting point and considers planning for 100%, 75%, and 50% of that effect. It assumes a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. For this binary outcome, the entries are participants per arm. The sample-size counts are very large because the observed risk difference is close to zero: planning to detect a smaller effect requires still more participants. These are planning illustrations, not the trial’s original design calculations or observed power.

The record does not report the trial’s original sample-size justification or the assumptions used when the study was designed. The illustration cannot establish whether the trial was adequately powered for the planned question. In general, power is a design property calculated for a specified effect and analysis, not a retrospective measure of whether a result is trustworthy. The planning entries should be interpreted only under the assumptions stated with them.

Why can over-dispersion matter?

General note: over-dispersion occurs when observed variation is greater than a statistical model expects. It can make standard errors too small if the model does not allow for that extra variation. The posted primary outcome is binary and lists no dispersion estimate, so this concern is not quantified in the registry record. The registry also does not describe a model for the primary outcome. No claim about over-dispersion in this trial can be made from the posted information.

10. Confidence Intervals and Precision

The risk-difference estimate is close to zero, while its confidence interval extends across zero and includes values in both directions. That span means the posted comparison is compatible with a lower recorded event proportion in either group, as well as little or no difference. The interval is the clearest indication of the uncertainty in the comparison; the unadjusted p-value of 0.912 is consistent with the absence of a clearly separated result under the posted comparison.

The confidence interval should not be treated as evidence of equivalence. Demonstrating equivalence or non-inferiority requires an appropriate design, a prespecified margin, and an analysis that addresses that question. The registry record does not report such a margin or an equivalence analysis. Nor does it post an interval for a time-to-event measure such as a hazard ratio.

Precision is also limited by the way the outcome is reported. The arm denominators are 134 and 131, and the outcome values are counts rather than a reported survival estimate over time. No follow-up distribution, censoring information, or missing outcome accounting is given. Those omissions make it difficult to judge how fully the counts represent the survival question. The confidence interval quantifies uncertainty for the posted contrast under its method; it does not account for unreported design or endpoint details.

In general, a larger study can produce a more precise estimate when other conditions are similar, but precision also depends on event frequency, follow-up, and analysis. The available results do not justify a claim that a clinically meaningful difference has been excluded. They show that the registry’s count-based comparison is uncertain and does not distinguish the groups clearly.

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 effect, not the trial’s original design. For this binary outcome, the figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario targets a stated fraction of the observed effect.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the chosen effect if that effect were the true one, under the stated assumptions and analysis. The 90% power column gives the corresponding number for a 90% chance. These are design calculations for hypothetical future studies, not a measure of the chance that the posted result is correct. This is not observed power.

The scenarios ask what sample size would be needed to plan for 100%, 75%, or 50% of the observed effect. As the target effect becomes smaller, more participants are needed to distinguish it from random variation. The displayed requirements are very large because the observed effect is close to zero. Such calculations are especially sensitive to the effect used as a planning target: an observed effect from a completed study may not be a stable estimate of the effect that a new study should target.

The registry record does not report the trial’s original sample-size justification, its planned effect size, or its planned power. The illustration should therefore not be read as a reconstruction of the trial design, and it does not establish that the completed trial did or did not meet its original statistical objectives.

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

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 = 0.374; treatment proportion p₁ = 0.381; average p̄ = 0.377.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6855 = 1.3435.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6855 = 0.5769.
4. n = (1.3435 + 0.5769)² / (0.0066)² = 85,933.7, rounded up to 85,934 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 <- 0.374045801526718                          # control proportion
p1 <- 0.380597014925373                          # 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(2093962)
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 = 85,934 (80% power), 115,041 (90% power)
 75% of observed effect: n per arm = 152,641 (80% power), 204,343 (90% power)
 50% of observed effect: n per arm = 343,147 (80% power), 459,376 (90% power)
power.prop.test: 85933.7 
Simulated power at n = 85,934 per arm: 0.802 (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.

13. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, comparisons, time points, or subgroup tests are evaluated. In general, the more tests performed, the greater the chance that at least one result appears unusual by chance. Researchers may address this through a prespecified hierarchy, adjustment, or other strategy. The registry record lists one primary outcome and no posted secondary outcomes, but that does not establish that no other outcomes or analyses were planned or conducted. The statistical analysis plan, multiplicity strategy, and full protocol are not reported in the registry record.

The comparison is labeled unadjusted, and no multiplicity adjustment is posted. The record does not say whether that comparison was prespecified, whether other analyses were performed, or how any additional testing was handled. The unadjusted p-value should therefore not be assumed to account for all possible analyses.

Missing data and analysis populations are also important. For an overall-survival outcome, general analysis depends on knowing participant follow-up and how participants without an observed event are handled. The record does not describe censoring, losses to follow-up, withdrawals, or the number included in an analysis of the primary outcome. It gives arm sizes and outcome counts, but does not identify an intention-to-treat, per-protocol, or other analysis population. These omissions limit assessment of whether the posted numbers include everyone randomized and how incomplete observation was addressed.

No interim analyses are described, and the registry record does not report whether any were planned or conducted. The reason for termination is also not reported. Without these details, it is not possible to assess whether decisions about stopping, testing, or analysis could have affected the interpretation of the outcome. These are limitations of the registry record, not proof that a particular procedure was or was not used.

14. 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: anaemia (5.4%), pulmonary embolism (3.8%), pneumonia (3.1%), respiratory failure (3.1%), overdose (3.1%).

The adverse-event summary lists serious adverse events in 52 of 130 participants at risk in the TH-302 and pemetrexed group, and in 72 of 130 participants at risk in the placebo and pemetrexed group. These are participant counts as recorded in the registry. They describe how many participants were reported as affected, not the number of separate event episodes or the duration of events.

The record also lists other adverse events in 130 of 130 participants at risk in each group. The definitions and collection period for these entries are not reported in the registry record. Death counts are not reported. A list of the top serious-event terms includes Anaemia (5.4%), Pulmonary embolism (3.8%), Pneumonia (3.1%), Respiratory failure (3.1%), Overdose (3.1%), and Respiratory tract infection (2.3%). The record does not assign these listed percentages to a particular arm in the information posted.

Safety counts are descriptive. Differences between groups cannot be interpreted without details about event definitions, observation periods, exposure, and the population included in safety reporting. The posted figures do not by themselves establish a causal relationship between a treatment and an event.

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

The posted results describe a randomized comparison of TH-302 plus pemetrexed against matching placebo plus pemetrexed. The primary outcome is named overall survival, with a 2 years timeframe. The registry lists counts of 51 and 49 participants in the two arms and gives an unadjusted p-value of 0.912 for a risk-difference comparison. Its confidence interval crosses zero, leaving the direction of the difference uncertain.

These results do not establish that the two regimens have equivalent effects. A non-significant comparison is not proof that the true difference is zero, and an interval that crosses zero may still include effects in either direction. The registry also does not post a survival curve, median survival, or hazard ratio, so the reported counts cannot answer how long participants lived or describe when events occurred.

The posted information cannot establish a treatment benefit or harm. The outcome event definition, time origin, censoring approach, and analysis population are not reported. There are no posted secondary outcomes or sponsor analyses, and the reason the study was terminated is not given. Consequently, the results should be read as a limited registry summary rather than a complete account of the trial’s statistical findings.

The adverse-event entries report serious-event counts in each group, along with a list of serious-event terms and percentages. They do not establish that an event was caused by treatment. Death counts are not reported, and definitions and observation periods are not described. The safety data therefore offer descriptive context but not a complete comparative safety analysis.

In general, a treatment comparison is most informative when the outcome definition, follow-up, analysis plan, and uncertainty are all clear. The posted record gives some comparative numbers, but important details needed to interpret the overall-survival question are absent. The appropriate statistical conclusion is limited: the recorded counts are similar in size, while the comparison remains imprecise and does not clearly distinguish the groups.

16. Why This Trial Matters Statistically

This trial raises several important statistical issues common to randomized oncology studies. First, overall survival is a time-to-event outcome, but the registry posts participant counts rather than a survival curve or another time-to-event estimate. That distinction matters because survival analysis uses when events occur and how long participants are followed, not only the number of participants in a category.

Second, the estimated risk difference is close to zero and its confidence interval spans both sides of the no-difference value. This illustrates why an estimate and its precision need to be considered together. A p-value of 0.912 alone does not demonstrate equivalence, and a non-significant finding is not proof that the treatments have identical effects. The interval indicates uncertainty in the direction and size of the count-based comparison.

Third, a randomized design does not remove the need for transparent reporting. The registry does not describe the primary analysis method, analysis population, missing-data handling, or original sample-size assumptions. These details are needed to judge how the outcome was analyzed and whether the posted comparison matches the trial’s planned question. The terminated status also makes the reason for stopping and its implications relevant, but the record does not report them.

Finally, the planning illustration shows how sample-size requirements can become large when the effect targeted for detection is small. It is a planning exercise based on the observed effect, not a retrospective verdict on the trial’s power. Together, these points distinguish the numerical result from what can responsibly be concluded from it: registry counts and a comparison are available, but a fuller statistical interpretation requires information the record does not include.

17. Limitations

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

The principal limitation is that overall survival is reported as participant counts without an explanation of what those counts represent. The record does not provide a survival curve, median survival, hazard ratio, event definition, time origin, or censoring rules. It therefore does not show the timing of events or the survival experience across follow-up.

The registry record does not report the statistical analysis plan, the primary test, the analysis population, or how missing outcome information was handled. It lists an unadjusted p-value but does not identify the test used. There are no posted secondary outcomes or additional analyses. The original sample-size justification and the reason for termination are also not reported.

For safety, the record gives participant counts at risk and affected, but does not describe event definitions, collection periods, exposure, or the analysis population. It does not report deaths, and the listed serious-event terms are not linked to a particular arm in the posted information.

These limitations do not show that the trial lacked appropriate methods; they mean that those methods and details cannot be evaluated from the registry record. Interpretation should remain within the bounds of the posted counts and comparison.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Study of TH-302 or Placebo in Combination With Pemetrexed in Patients With Non-squamous Non-small Cell Lung Cancer — NCT02093962.
• Registry record last updated 2025-05-16; status last verified 2025-05.
• Results first posted 2017-08-11.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

21. Record Summary

NCT02093962 is a randomized phase 2 parallel-group study of TH-302 plus pemetrexed versus matching placebo plus pemetrexed for advanced non-squamous non-small cell lung cancer in the second-line setting. The official title describes a double-blind, placebo-controlled, multicenter study; the registry design fields list triple masking. Enrollment is recorded as 265, with 134 participants in the TH-302 group and 131 in the placebo group. The study started in 2014-06, reached primary completion in 2016-04, and is listed as terminated.

Overall survival over 2 years is the primary outcome. The registry posts participant counts of 51 and 49, a risk-difference comparison with a confidence interval crossing zero, and an unadjusted p-value of 0.912. No outcome analyses or secondary outcomes are posted. Serious adverse-event counts are 52 of 130 and 72 of 130; the reason for termination and key analysis details are not reported in the registry record.