A Study of Efficacy and Safety of Fruquintinib (HMPL-013) in Participants With Metastatic Colorectal Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of Efficacy and Safety of Fruquintinib (HMPL-013) in Participants With Metastatic Colorectal Cancer (NCT04322539), a randomized phase 3 study. The primary outcome is Overall Survival (OS).

2. Clinical Question

3. Trial Design

This was a randomized, parallel-group, phase 3 trial with a placebo comparator. The registry record describes the allocation as randomized, the model as parallel, and the masking as quadruple. Its brief summary also calls the study double-blind; the registry record does not explain how those masking descriptions relate to one another. The trial was global, multicenter, and completed. The enrollment field records 691 participants, and the brief summary says randomization followed a 2:1 ratio to fruquintinib plus best supportive care or placebo plus best supportive care.

The two groups received matching oral study treatments with best supportive care. Both regimens were specified as once daily for 3 weeks followed by a 1-week break in each 28-day cycle. The record describes the active dose as fruquintinib 5 mg and the placebo dose as 5 mg. Treatment duration, treatment discontinuation rules, and the details of best supportive care are not reported in the registry record.

The primary endpoint was overall survival in the intention-to-treat population, which the record defines as all randomized participants. The endpoint measured time from randomization to death from any cause. Participants without a death report at analysis were censored at their last-known-alive date. The stated timeframe was up to 22 months. The primary comparison was reported as a stratified hazard ratio using a stratified log-rank test.

The registry lists primary completion on 2022-07-29 and status as completed; the recorded start date was 2020-08-12. The number of participants in each analysis population beyond the reported outcome-specific group counts, the randomization strata, and details of the statistical analysis plan are not reported in the registry record. The trial’s original sample-size justification and its intended event target are also not reported in the registry record.

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.

Before assignment: A total of 691 participants were randomized and enrolled in this study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT population included all randomized participants.

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: Intent-to-Treat (ITT) population included all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival (OS), measured over From date of randomization to death from any cause (up to 22 months).

Overall survival measures the time from randomization until death from any cause. The registry defines the endpoint from randomization to death and states that participants not reported dead at analysis were censored at the date they were last known to be alive. Its stated observation timeframe was up to 22 months. The registry describes the primary population as the intention-to-treat population, including all randomized participants.

General: An all-cause time-to-event endpoint captures deaths regardless of their attributed cause. It can account for the timing of events as well as whether an event was recorded during follow-up. Censoring allows a participant’s observed follow-up to contribute information up to the last time they were known alive when no death had been reported by analysis; it does not establish what happened after that date.

The registry reports median overall survival for each randomized group and a hazard ratio comparing the groups. A median describes the time by which half of the group’s observed survival distribution has reached the event, subject to the endpoint’s analysis and censoring. The hazard ratio gives a relative comparison of event rates over follow-up under the analysis model; it is not a difference in median survival time. The registry’s description of the endpoint calculation specifies the date arithmetic used to express time in months. The method used to estimate the medians and their confidence intervals is not reported in the registry record.

7. Results Posted in the Registry

• Fruquintinib + BSC Group vs Placebo + BSC Group: hazard ratio 0.66 (95% CI 0.55–0.80), reported p < 0.001 (as reported in the registry).

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Progression Free Survival (PFS), as Assessed by the Investigator Using Response Evaluation Criteria In Solid Tumors (RECIST) v1.1

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (stratified log-rank test); it was not recalculated.
• Result:
  • Fruquintinib + BSC Group vs Placebo + BSC Group: hazard ratio 0.32 (95% CI 0.27–0.39), reported p < 0.001 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the hazard of the event is statistically lower for Fruquintinib + BSC Group vs Placebo + BSC Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Objective Response Rate (ORR) Per Response Evaluation Criteria in Solid Tumors Version 1.1 (RECIST 1.1)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Fruquintinib + BSC Group: 1.5% (7/461) versus 0.0% (0/230) on control; risk difference 1.5 percentage points (95% CI 0.4 to 2.6); unadjusted two-proportion z-test p = 0.060.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fruquintinib + BSC Group and the control. The interval gives the range of effects that remain compatible with the data.

Disease Control Rate (DCR) Per Response Evaluation Criteria in Solid Tumors Version 1.1 (RECIST 1.1)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Fruquintinib + BSC Group: 55.5% (256/461) versus 16.1% (37/230) on control; risk difference 39.4 percentage points (95% CI 32.9 to 46.0), risk ratio 3.45 (2.54–4.69); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Fruquintinib + BSC Group than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes address several aspects of disease course and response: investigator-assessed progression-free survival, objective response rate, disease control rate, and other registered outcomes including duration of response and adverse events. The posted numerical secondary results include progression-free survival and response and disease-control rates. Their definitions and analysis scales differ from overall survival, so they provide complementary information rather than repeated measures of the primary endpoint.

At a broad level, the reported secondary time-to-event comparison points in the same direction as the primary overall-survival comparison. The response-related outcomes also describe a between-group contrast, but they do not measure time to death. This pattern can be considered alongside the primary result without treating one endpoint as proof of another. The outcome-specific estimates and intervals remain essential because different endpoints can have different uncertainty and interpretation.

Secondary outcomes generally warrant more caution when multiple outcomes are assessed. If many hypotheses are tested, the chance of at least one apparently strong result can increase unless the analysis plan controls that risk. The registry record lists 16 outcome measures and 11 analyses, but does not report a multiplicity adjustment strategy, a hierarchy for testing secondary outcomes, or which analyses were confirmatory. Therefore, the secondary p-values should not automatically be read as having the same confirmatory status as the primary test.

Some registered secondary outcomes do not have numerical results included in the registry record for this analysis. Their results are not reported in the registry record. A missing posted numerical result should not be interpreted as evidence of no effect or as evidence of benefit. The overall pattern across available secondary endpoints can add context, but the primary endpoint remains the prespecified focus identified in the registry record.

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

• Progression Free Survival (PFS), as Assessed by the Investigator Using Response Evaluation Criteria In Solid Tumors (RECIST) v1.1
• Objective Response Rate (ORR) Per Response Evaluation Criteria in Solid Tumors Version 1.1 (RECIST 1.1)
• Disease Control Rate (DCR) Per Response Evaluation Criteria in Solid Tumors Version 1.1 (RECIST 1.1)
• Duration of Response (DOR) Per Response Evaluation Criteria in Solid Tumors Version 1.1 (RECIST 1.1)
• Number of Participants With Treatment-emergent Adverse Events (TEAEs) and Serious TEAEs
• Observed Plasma Concentrations of Fruquintinib and Metabolite M11
• Change From Baseline of Electrocardiogram (ECG) Results - QTcF Intervals Using Fridericia's Formula
• Change From Baseline of ECG Results -QTcB Intervals Using Bazzett's Formula

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary hazard ratio compare?

The registry reports a stratified hazard ratio of 0.662 for fruquintinib plus best supportive care versus placebo plus best supportive care. Its 95% confidence interval is 0.549 to 0.800, and the reported p-value is < .001. The method is identified as a stratified log-rank test. The registry does not identify the stratification factors, so their role cannot be described more specifically from the record.

General: A hazard is an event rate among participants who have not yet experienced the event at a given point in follow-up. A hazard ratio compares those rates between groups over time within a model. It is not a ratio of the medians and should not be read as a direct change in an individual participant’s survival time. A hazard ratio also summarizes the comparison rather than showing when events occurred or how the curves behaved throughout follow-up.

What does the stratified log-rank test do?

The registry names the stratified log-rank test as the method for the primary comparison. General: A log-rank test compares time-to-event experience across groups while using event timing and censoring information. A stratified version carries out that comparison across specified strata and combines information across them. Stratification can account for the design’s chosen factors in the comparison, but the factors and their implementation are not reported in the registry record. The test’s p-value addresses compatibility with its null hypothesis under the analysis assumptions; it does not measure the probability that the observed result arose by chance in an everyday sense, or the probability that a treatment effect is true.

How should medians and censoring be understood?

The registry reports median survival and 95% confidence intervals by group, and specifies that participants without a reported death at analysis were censored at the date last known alive. General: Censoring means that the event time is not observed beyond the last known follow-up point. Time before censoring still contributes information, but censoring is not the same as a death or proof that a participant remained alive afterward. Estimating survival in the presence of censoring generally requires a time-to-event method. The particular method used to estimate the medians and their intervals is not reported in the registry record, so it should not be assumed from the endpoint description alone.

What do confidence intervals and p-values convey?

General: A confidence interval expresses uncertainty about an estimated parameter under a statistical procedure. Its width reflects precision in the context of that procedure; it is not a range containing a specified proportion of individual participant outcomes. A p-value describes how incompatible the observed data are with a stated null model, conditional on the assumptions and analysis. It is not an effect-size measure and does not determine clinical importance. The registry reports 95% confidence intervals for the primary medians and hazard ratio and reports p < .001 for the hazard-ratio comparison.

How are the secondary comparisons different?

The posted secondary outcomes include investigator-assessed progression-free survival, objective response rate, and disease control rate. The time-to-event comparison for progression-free survival is reported using a stratified log-rank test and a hazard ratio. The response-rate analyses have sponsor-reported adjusted differences using the Cochran-Mantel-Haenszel method. These outcomes use different definitions and analysis methods, so their estimates are not interchangeable with the primary overall-survival estimate.

Some simple comparisons in the planning material are described as unadjusted recalculations from posted summary statistics. General: An unadjusted calculation does not reproduce an analysis that accounts for stratification or other model features. Where both are available, the sponsor’s reported analysis is the primary source for the trial’s inferential result. These recalculations can help readers understand the scale of a contrast, but should not replace the reported analysis.

What is not specified?

The registry record does not report the complete statistical analysis plan, the original sample-size justification, the trial’s planned interim analyses, the handling of every missing-data scenario, or details of model diagnostics. The fact that a method is named for an endpoint does not supply those missing details. General explanations in this discussion describe statistical concepts; they do not assert that unreported procedures were used in this trial.

11. Confidence Intervals and Precision

The primary group estimates are medians with 95% confidence intervals. For fruquintinib plus best supportive care, the median overall survival was 7.4 months, with an interval from 6.7 to 8.2 months. For placebo plus best supportive care, it was 4.8 months, with an interval from 4.0 to 5.8 months. The reported hazard ratio was 0.662, with a 95% confidence interval from 0.549 to 0.800.

General: A confidence interval communicates uncertainty about an estimate under the method that generated it. A narrower interval indicates greater precision on the scale of that estimate, while a wider one indicates more uncertainty. The interval is not a prediction range for individual participants and does not mean that a specified proportion of participant survival times lies inside it.

The hazard-ratio interval is entirely below 1, consistent with the reported direction of the comparison and the p-value of < .001. This interval concerns the hazard ratio, not the difference between the group medians. The intervals around the two medians are separate estimates; their overlap or separation is not a substitute for the formal comparative analysis. The registry’s reported stratified log-rank result is the appropriate source for the primary inferential comparison.

Precision also depends on the information available for analysis, follow-up, and the statistical method. The registry record supplies group counts and confidence intervals, but does not provide the full event-time data, detailed censoring patterns, or the method used to calculate the median intervals. That limits independent assessment of how precision was obtained. The intervals quantify statistical uncertainty, but do not address uncertainty about generalizability, unreported analysis decisions, or clinical importance.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not the trial’s original design assumptions. For time-to-event outcomes, the listed quantities are total events, not participants per arm. For other outcomes, the quantities are participants per arm. Thus, the overall-survival planning figures refer to total events, whereas the disease-control-rate figures refer to participants per arm. The planning material states a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers effects equal to 100%, 75%, and 50% of the observed effect.

The 80% power column represents the planning number associated with an 80% chance of rejecting the null hypothesis if the assumed effect and the planning assumptions hold. The 90% power column describes the corresponding planning number for a 90% chance under those assumptions. These are design calculations, not measurements of how likely the trial’s result was to be significant after it was completed. This is not observed power.

For overall survival, the listed total-event requirements at 80% power are 185 for planning at 100% of the observed effect, 329 at 75%, and 739 at 50%. At 90% power, the corresponding listed total-event requirements are 248, 440, and 989. These values are event counts for planning, not participants per group. For disease control rate, the listed participants per arm at 80% power are 22, 38, and 77 for the respective effect fractions; at 90% power, they are 29, 50, and 102.

Smaller assumed effects require more information to detect under the stated planning framework, which is why the illustrations increase as the assumed fraction of the observed effect gets smaller. The trial’s own original sample-size rationale and assumptions are not reported in the registry record. These illustrations should not be mistaken for evidence that the study was designed around those assumptions or that its achieved power was one of the displayed values.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

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 = 0.662, so ln(HR) = -0.4125.
2. d = 4 × (1.96 + 0.842)² / [ln(0.662)]² = 184.5, rounded up to 185 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 <- 0.662                              # 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(4322539)
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 = 185 (80% power), 248 (90% power)
 75% of observed effect: events = 329 (80% power), 440 (90% power)
 50% of observed effect: events = 739 (80% power), 989 (90% power)
Simulated power with 185 events: 0.811 (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.

14. 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 273 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 691 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 <- 4.8          # control-arm median, months (converted from the posted unit)
hr          <- 0.662          # 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: 166         p (1-sided)   0.0001
  Events: 84        ~HR at bound   0.4430
   Month: 15    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.66   0.0338
   IA 2: 67%                   Z   2.5114
      N: 266         p (1-sided)   0.0060
 Events: 167        ~HR at bound   0.6773
   Month: 23    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.66   0.5603
       Final                   Z   1.9930
      N: 274         p (1-sided)   0.0231
 Events: 250        ~HR at bound   0.7769
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.66   0.9000



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

15. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparison as a stratified hazard ratio of 0.662, with a 95% confidence interval from 0.549 to 0.800 and p < .001 using a stratified log-rank test. The same reported result is listed in the outcome analysis information. There is no discrepancy flagged between the posted primary result and the reported analysis, so the sponsor’s own analysis is the relevant inferential result for the trial.

General: A recalculation from group-level summaries is necessarily limited compared with an analysis using the full participant-level data and the specified trial method. It may not reproduce stratification, censoring, covariate handling, or other analysis features. Consequently, an unadjusted recalculation can be useful as a check or explanatory aid, but it does not supersede a reported trial analysis. The primary result should be interpreted using the sponsor-reported method and estimate, not an independently reconstructed contrast.

For the binary secondary endpoints, the registry lists sponsor-reported adjusted differences using the Cochran-Mantel-Haenszel method. Simple unadjusted recalculations based on posted group summaries are not identical in method to those adjusted analyses. Where values differ in precision or inferential result, the sponsor-reported analysis takes precedence as the trial’s stated analysis. The registry does not provide all details needed to reconstruct the adjusted analyses independently.

16. Multiplicity, Missing Data and Analysis Populations

The registry identifies overall survival as the primary outcome and lists numerous secondary outcomes, including progression-free survival, response rates, duration of response, adverse events, plasma concentrations, and ECG measures. It records 16 outcome measures and 11 analyses. The registry record does not report whether the secondary hypotheses were arranged in a formal testing hierarchy, whether p-values were adjusted for multiple testing, or which secondary analyses were designated confirmatory.

General: When several outcomes or hypotheses are examined, interpreting each p-value as if it were the only test can overstate the strength of the overall evidence. Multiplicity procedures can control error rates across a family of planned tests, but the appropriate approach depends on the trial’s aims and analysis plan. Without a reported strategy, secondary p-values are best treated as supportive or exploratory rather than automatically equivalent in evidential status to the primary result.

The primary population is described as the intention-to-treat population, including all randomized participants. The overall-survival endpoint has an explicit censoring rule for participants without a death report at analysis. However, the registry record does not provide detailed missing-data procedures for the secondary outcomes, the amount or pattern of missing data, or sensitivity analyses for the primary endpoint. Those omissions limit assessment of how incomplete outcome information may have affected estimates.

The record also does not report planned interim analyses, stopping rules, or the complete statistical analysis plan. Their absence from the registry record does not establish that such procedures were or were not used; those details are simply not reported in the registry record. The posted primary result can be interpreted according to its named method, while these missing design and analysis details limit a fuller audit of prespecification and robustness.

The stated intention-to-treat definition is relevant because it preserves the randomized comparison in principle. The outcome-specific group counts are recorded for analyses, but the registry record does not explain differences between the enrollment count and the analysis denominators. No assumptions about reasons for exclusions, missing assessments, or treatment adherence should be inferred from those counts alone.

17. Safety Results

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

Deaths

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: disease progression (12.2%), intestinal obstruction (2.6%), general physical health deterioration (2.2%), ileus (2.2%), pneumonia (2.0%).

The registry’s serious-event figures list 173 affected participants among 456 at risk in the fruquintinib plus best supportive care group, and 88 among 230 at risk in the placebo plus best supportive care group. The figures for other treatment-emergent adverse events list 446 among 456 at risk in the fruquintinib group and 205 among 230 at risk in the placebo group. These are reported counts and denominators; they are not adjusted comparisons, and no new percentages are calculated.

The registry also lists deaths of 411 and 203 in the respective groups. These death counts should not be treated as a separate cause-specific safety comparison: overall survival counts death from any cause, and the registry record does not give a causal attribution for these deaths in the safety summary.

The most frequently listed serious-event terms include disease progression (12.2%), intestinal obstruction (2.6%), general physical health deterioration (2.2%), ileus (2.2%), pneumonia (2.0%), and abdominal pain (1.5%). The registry record does not provide the term-specific denominators or enough detail to determine attribution from these figures alone. Serious adverse-event counts describe reported events within the trial; they do not by themselves establish that a study treatment caused an event or allow a complete benefit-risk assessment.

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

The primary result is a randomized comparison of fruquintinib plus best supportive care with placebo plus best supportive care in participants with refractory metastatic colorectal cancer. The registry reports median overall survival of 7.4 months in the fruquintinib group and 4.8 months in the placebo group, alongside a sponsor-reported hazard ratio of 0.662 with a 95% confidence interval from 0.549 to 0.800 and p < .001. These quantities summarize the trial’s primary endpoint using different statistical measures.

The hazard ratio and its interval describe a group-level comparison over follow-up under the reported analysis. They do not say how long any individual participant will live, and they are not a guarantee of an outcome for a particular person. The median values are also group summaries, not individual predictions. Statistical evidence against the null hypothesis does not by itself determine whether the magnitude is clinically important; the registry record does not state a threshold for clinical importance.

The comparison is between two regimens that both included best supportive care. It therefore does not estimate best supportive care versus no care, nor does it separate the contribution of best supportive care from the assigned study treatment. The findings concern the enrolled trial population and do not automatically generalize to groups not described by the eligibility information available in the registry record.

The posted endpoint is overall survival from randomization to death from any cause, with censoring at last known alive for participants without a death report at analysis. The result does not show every participant’s follow-up, the full timing of events, or the causes of deaths. The record’s timeframe is up to 22 months, which does not imply uniform follow-up.

Secondary outcomes may add context about disease progression and response, but they use different definitions and may be affected by multiplicity. Missing details about the complete statistical plan, missing-data handling, and secondary testing strategy limit conclusions beyond the named primary analysis. Safety counts likewise describe reported events and should not be read as proof of causal attribution.

19. Why This Trial Matters Statistically

This trial illustrates how time-to-event results combine a median summary with a relative comparison. The medians describe the timing of the survival distribution within each group, while the hazard ratio compares event rates over follow-up under the reported analysis. Keeping these quantities distinct prevents a hazard ratio from being misread as a direct difference in months or as an individual-level prediction.

The analysis also highlights why the method and analysis population matter. The registry identifies an intention-to-treat population and a stratified log-rank test for the primary comparison. The treatment contrast is randomized and uses a placebo-plus-best-supportive-care comparator, making the comparison specific to those assigned regimens. At the same time, stratification details and the full statistical analysis plan are not reported, limiting independent reproduction of the sponsor’s analysis.

The record offers an opportunity to read primary and secondary findings in context. Overall survival is the primary endpoint, while progression-free survival and response outcomes address related but distinct questions. Considering a coherent pattern can be informative, but multiple outcome testing means secondary results should not simply be granted the same evidential weight as the primary analysis when the multiplicity strategy is unreported.

Finally, planning illustrations show how assumed effect size and desired power affect the amount of information a future study may require. They are not evidence of the trial’s original design rationale or achieved power. Separating those planning calculations from observed trial results is important for statistical interpretation and for avoiding retrospective claims about design adequacy.

20. 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 does not provide detailed eligibility criteria, so the precise boundaries of the enrolled population cannot be evaluated from this record alone. Although the trial is described as global and multicenter, the participating locations and representation of population subgroups are not reported in the registry record. Generalizability beyond the described refractory metastatic colorectal cancer population therefore cannot be assessed in detail.

The primary endpoint timeframe is listed as up to 22 months, but the record does not provide follow-up distribution, the number and timing of deaths at analysis, or the pattern of censoring. Those details would help readers assess the maturity and completeness of the time-to-event information. The method used to estimate the median confidence intervals and the stratification factors used in the primary analysis are also not reported in the registry record.

The record names the primary test and reports the primary estimate, but does not include the complete statistical analysis plan, original sample-size rationale, interim analysis plan, or stopping rules. It also does not report a multiplicity strategy for the many listed outcomes. These omissions limit independent assessment of prespecification and the confirmatory status of secondary findings.

Although the record defines the intention-to-treat population and states the censoring rule for overall survival, detailed missing-data procedures and sensitivity analyses are not reported. The record does not explain differences between the enrollment count and outcome-specific analysis denominators. Treatment exposure, adherence, discontinuation, and reasons for withdrawal are not reported in the registry record.

The safety summary includes group counts and selected serious-event terms, but does not provide the details needed to establish causality or fully compare event types and timing. Together, these reporting limits do not invalidate the posted primary analysis, but they constrain what can be independently checked and how broadly its findings can be interpreted.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: A Study of Efficacy and Safety of Fruquintinib (HMPL-013) in Participants With Metastatic Colorectal Cancer — NCT04322539.
• Registry record last updated 2025-04-04; status last verified 2025-03.
• Results first posted 2023-09-14.
• 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.

24. Record Summary

The registry describes a completed, randomized, parallel-group phase 3 trial comparing fruquintinib plus best supportive care with placebo plus best supportive care in refractory metastatic colorectal cancer. The brief summary reports 691 randomized participants assigned in a 2:1 ratio. The primary endpoint was overall survival in the intention-to-treat population, defined as time from randomization to death from any cause.

The registry reports median overall survival of 7.4 months for fruquintinib plus best supportive care and 4.8 months for placebo plus best supportive care. The sponsor-reported stratified hazard ratio was 0.662, with a 95% confidence interval from 0.549 to 0.800 and p < .001. Secondary outcomes include progression-free survival and response measures, while safety information includes serious-event counts and selected reported terms.

The registry record does not report the complete statistical analysis plan, original sample-size justification, multiplicity strategy, or detailed missing-data procedures. Planning illustrations based on observed effects should be distinguished from the trial’s original design assumptions and from observed trial results.