Comparing Efficacy and Safety of Stivant (AryoGen Bevacizumab) Versus Avastin in Metastatic Colorectal Cancer: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Comparing Efficacy and Safety of Stivant (AryoGen Bevacizumab) Versus Avastin in Metastatic Colorectal Cancer (NCT03288987), a randomized phase 3 study. The primary outcome is Progression Free Survival (PFS).

2. Clinical Question

3. Trial Design

The registry describes a Phase III, randomized, parallel-group, active-controlled trial in metastatic colorectal cancer. The brief summary characterizes it as a two-arm, double-blind study, with patients and assessors blinded, and an allocation ratio of 2:1. The registry’s masking field says double, while the official title says triple blinded. The record does not clarify this difference. The listed enrollment is 126, and the trial status is completed.

Both arms received bevacizumab with FOLFIRI-3. The AryoGen Pharmed arm used its bevacizumab product, while the comparator arm used Roche bevacizumab, identified as Avastin. The arm descriptions specify bevacizumab 5 mg/kg every 2 weeks in both groups. The active-control design makes the central comparison between products within the same described chemotherapy combination.

The registry lists a start date of 2016-10-04 and a primary completion date of 2018-07-30. It reports six outcome measures and five analyses. The primary endpoint was progression-free survival; listed secondary outcomes include overall survival, objective response rate, time to treatment failure, adverse events, and anti-drug antibody samples. Detailed results in the record cover only some of those outcomes.

The official title refers to AryoGen trastuzumab, whereas the brief summary, intervention and arm descriptions identify bevacizumab. The trial title also describes Stivant. This inconsistent naming is a record-level limitation; the treatment comparison described in the trial summary and arms is AryoGen Pharmed bevacizumab versus Roche bevacizumab, each with FOLFIRI-3.

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 population assessable for PFS was per protocol.

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 Progression Free Survival (PFS), measured over PFS was measured from the start of chemotherapy to the date of disease progression or to the date of death if no progression whichever came first, assessed up to 12 months.

Progression-free survival (PFS) measures the time from randomization to documented disease progression or death from any cause, whichever occurs first. The registry’s timeframe describes measurement from the start of chemotherapy to progression or death, assessed up to 12 months; its endpoint definition instead begins at randomization. This difference in stated starting point is not reconciled in the registry record. Progression was assessed by the investigator.

PFS is a time-to-event outcome: it uses both whether an event occurred and the time until that event. It is used to describe how long participants remain alive without documented progression during follow-up. A median is the time by which half of the relevant observed survival distribution has experienced the event, under the methods used to estimate it. It does not describe every participant’s experience, and it is not the same as a mean follow-up time.

The registry reports median PFS of 232.0 days for AryoGen Pharmed bevacizumab and 210.0 days for Roche bevacizumab. The primary population is described as per protocol. The registry gives a standard error of 12.21 for the Roche arm but no spread measure for the AryoGen arm. The sponsor’s comparative analysis is a Cox regression hazard ratio, which summarizes the relative event rate over follow-up under the model; it is not a direct comparison of the two medians.

7. Results Posted in the Registry

• Bevacizumab + FOLFIRI-3 (AryoGen Pharmed Bevacizumab) vs Bevacizumab + FOLFIRI-3 (Roche Bevacizumab): hazard ratio 0.79 (95% CI 0.46–1.35), reported p = 0.470 (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.

Overall Survival (OS)

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Bevacizumab + FOLFIRI-3 (Roche Bevacizumab): 38.6% (17/44) versus 36.6% (30/82) on control; risk difference 2.1 percentage points (95% CI -15.7 to 19.8), risk ratio 1.06 (0.66–1.69); unadjusted two-proportion z-test p = 0.820.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bevacizumab + FOLFIRI-3 (Roche Bevacizumab) and the control. The interval gives the range of effects that remain compatible with the data.

Objective Response Rate

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Bevacizumab + FOLFIRI-3 (Roche Bevacizumab): 21.7% (5/23) versus 40.5% (17/42) on control; risk difference -18.7 percentage points (95% CI -41.2 to 3.7), risk ratio 0.54 (0.23–1.27); unadjusted two-proportion z-test p = 0.127.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bevacizumab + FOLFIRI-3 (Roche Bevacizumab) and the control. The interval gives the range of effects that remain compatible with the data.

Time to Treatment Failure

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Regression, Cox); it was not recalculated.
• Result:
  • Bevacizumab + FOLFIRI-3 (AryoGen Pharmed Bevacizumab) vs Bevacizumab + FOLFIRI-3 (Roche Bevacizumab): hazard ratio 1.11 (95% CI 0.76–1.61), reported p = 0.590 (as reported in the registry).
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between Bevacizumab + FOLFIRI-3 (AryoGen Pharmed Bevacizumab) vs Bevacizumab + FOLFIRI-3 (Roche Bevacizumab) and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes provide additional descriptions of survival, response, treatment failure, and safety, but they do not replace the primary PFS comparison. The registry lists five secondary outcome categories, while detailed numeric results are posted for only some of them. In particular, the record names adverse events and anti-drug antibody samples as secondary outcomes, but does not give a complete set of comparative results for every listed outcome in the material summarized by the registry.

Across the detailed secondary analyses, the reported estimates and tests use different methods: Cox regression for time-to-treatment-failure and overall survival, and Fisher’s Exact Test for objective response. This methodological diversity reflects different outcome types, but it also means the results are not a single coherent confirmatory test. The primary PFS analysis remains the main endpoint for the trial’s stated central question.

Secondary findings can help describe whether patterns across outcomes appear broadly consistent, but any apparent alignment or difference should be interpreted cautiously. The registry does not report a prespecified hierarchy, a multiplicity adjustment, or a plan for handling multiple secondary comparisons. General statistical point: when several hypotheses are tested, the chance of at least one apparently notable result can increase, even if none reflects a real effect. Unadjusted secondary results therefore carry less confirmatory weight than a prespecified primary analysis.

These secondary outcomes also differ in analysis populations and available precision. The posted summaries do not establish that the same participants contributed to every endpoint, and the endpoint definitions and missing-data procedures are not fully described. As a result, secondary outcomes can contextualize the primary result but cannot resolve its uncertainty or demonstrate the trial’s non-inferiority objective in the absence of the margin and decision rule.

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

• Overall Survival (OS)
• Objective Response Rate
• Time to Treatment Failure
• Incidence of the Adverse Events
• Number of Positive Anti-drug Antibody (ADA) Samples Among Patients (Immunogenicity)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary comparison uses Cox regression, a method for time-to-event data. Rather than compare only the two median PFS values, Cox regression uses the observed event times and accounts for participants whose event time is not observed during the study period, subject to the analysis’s censoring assumptions. The registry reports a hazard ratio of 0.79 for AryoGen Pharmed bevacizumab versus Roche bevacizumab. A hazard ratio is a relative summary of event rates over follow-up under the model; it is not a risk ratio, a difference in median days, or the probability that one participant will experience progression before another.

A hazard ratio below 1 indicates a lower estimated event hazard in the first-listed arm relative to the second-listed arm under the fitted model; a value above 1 indicates a higher estimate. This direction does not by itself establish a treatment effect. The confidence interval and the assumptions behind the analysis matter, and the registry record does not report the model covariates, proportional-hazards assessment, censoring details, or missing-data procedures.

The registry reports a 90% confidence interval for the primary hazard ratio and p = 0.47. A confidence interval describes the range of values compatible with the data under the analysis and its assumptions. It is not a probability statement that the true value lies in the particular interval. A p-value measures how incompatible the data are with a specified null hypothesis under the test assumptions; it does not measure the probability that the null hypothesis is true. Neither quantity alone determines whether a non-inferiority objective was met. That judgment requires the non-inferiority margin and the prespecified analysis rule, which are not reported in the registry record.

Several secondary outcomes are binary counts, including overall survival as posted and objective response rate. A risk difference expresses the difference between the proportions in the two groups. The recalculated intervals and p-values for these outcomes are unadjusted comparisons from posted summaries; they are not the sponsor’s adjusted analyses. General statistical point: unadjusted comparisons do not account for testing multiple outcomes, so their p-values can overstate how compelling a finding is when many outcomes are examined. The record does not report a multiplicity adjustment or a hierarchy for secondary outcomes.

The registry’s own analyses must be kept distinct from simple recalculations. For overall survival, it reports a Cox regression hazard ratio of 0.99, a 95% confidence interval from 0.55 to 1.80, and p = 0.99. For objective response rate, it reports Fisher’s Exact Test with p = 0.17. For time to treatment failure, it reports a Cox regression hazard ratio of 1.11, a 95% confidence interval from 0.76 to 1.61, and p = 0.59. These are sponsor-reported analyses as posted; the simple risk-difference recalculations are not substitutes for them.

Fisher’s Exact Test is a method for comparing categorical outcomes, particularly useful when the observed counts are limited. It evaluates the compatibility of the table of event and non-event counts with a null of no association, under its testing framework. The registry provides a p-value but no sponsor-reported effect estimate or interval for the objective response analysis. General statistical point: a p-value without an effect estimate and uncertainty interval gives limited information about the size and precision of a difference.

Median time-to-event summaries describe the estimated time at the midpoint of the event-time distribution. Standard errors, where reported, convey uncertainty in an estimate under the method used; they are not participant-level variability or confidence intervals. The primary record gives no spread for the AryoGen median and reports a standard error of 12.21 for the Roche median. A comparative hazard ratio is a separate model-based quantity and should not be inferred from the medians.

General statistical point: over-dispersion arises when count variability exceeds what a model assumes. It can make standard errors too small and tests too optimistic if ignored. The registry does not report a count model for the primary endpoint, so over-dispersion is not a stated issue for the Cox analysis. More generally, the published summary does not identify enough model details to assess all assumptions independently.

The primary endpoint population is described as per protocol, meaning that the reported endpoint analysis was restricted according to a protocol-defined set of participants. The criteria defining that set are not reported in the registry record. The record also does not report an intention-to-treat PFS analysis, the handling of protocol deviations, or how missing endpoint data were treated. These omissions matter especially in a non-inferiority trial, where analysis-population choices can affect interpretation.

11. Confidence Intervals and Precision

The primary hazard ratio is 0.79, with a 90% confidence interval from 0.46 to 1.35. The interval is broad enough to include values below and above 1. It therefore allows materially different relative event-rate interpretations, rather than pinning down a narrow estimate. The point estimate is only one value within this range and should not be treated as exact.

Confidence intervals express statistical uncertainty under the analysis method and assumptions. They do not include every source of uncertainty, such as ambiguity in the record’s endpoint timing language, the lack of reported model details, or possible limitations in how outcomes were collected. The registry does not report a confidence interval for either PFS median. It reports a standard error of 12.21 for the Roche median and no spread measure for the AryoGen median, so the precision of the two arm-specific medians cannot be fully compared from the posted summaries.

The sponsor’s primary confidence interval is at the 90% level. A different confidence level would generally yield a different interval; the 95% intervals reported for some secondary Cox analyses should not be conflated with the primary interval. The primary p-value, 0.47, does not narrow the interval or settle the non-inferiority question. The non-inferiority margin is not reported in the registry record, so the relationship between the interval and the intended decision threshold cannot be assessed.

Precision is also affected by the analysis population and event information, not just total enrollment. The registry lists enrollment of 126, while the PFS arm summaries give participant counts of 72 and 40. The reason these counts differ from overall enrollment is not reported in the registry record. The posted summaries do not give the number of PFS events or detailed follow-up distribution, limiting assessment of how much information supports the time-to-event estimate.

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 sample-size figures are planning illustrations based on the observed effect, not the trial’s original design calculations. For the time-to-event outcomes, the figures are total events required across groups, not participants per arm. For the binary outcomes, the figures are participants per arm. The planning assumptions listed are a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The time-to-event illustrations use the Schoenfeld approach.

The 80% power column describes a planning scenario in which a study designed under those assumptions would have an 80% chance of detecting the specified effect at the stated significance level, if that effect were the true one and the assumptions held. The 90% column uses a higher target chance of detection. Neither column describes the probability that the observed result is true, nor does it indicate the power achieved by the completed trial. These calculations are not observed power.

Each row scales the effect used for planning: 100%, 75%, or 50% of the observed effect. A smaller effect is harder to distinguish from random variation, so the corresponding planning requirement is larger. This pattern is visible in both event-based and participant-based illustrations. The required scale can be very different depending on the endpoint and effect used; the numbers should be read in the units stated for that outcome, not compared as if every row measured the same thing.

The trial’s own sample-size justification, design effect, assumptions about event accrual, and original power target are not reported in the registry record. These illustrations are therefore not evidence that the trial was adequately or inadequately sized. They are hypothetical planning references derived from the posted observed effects and should not be read as a retrospective test of study quality.

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 = 0.790, so ln(HR) = -0.2357.
2. d = 4 × (1.96 + 0.842)² / [ln(0.790)]² = 565.0, rounded up to 566 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 <- 0.79                              # 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(3288987)
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 = 566 (80% power), 757 (90% power)
 75% of observed effect: events = 1,005 (80% power), 1,345 (90% power)
 50% of observed effect: events = 2,261 (80% power), 3,026 (90% power)
Simulated power with 566 events: 0.792 (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 861 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 126 participants.

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

R code and output

suppressWarnings(suppressMessages({ library(gsDesign); library(rpact) }))
med_control <- 6.9041095890411          # control-arm median, months (converted from the posted unit)
hr          <- 0.79          # 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: 570         p (1-sided)   0.0001
 Events: 255        ~HR at bound   0.6282
   Month: 16    P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.79   0.0338
   IA 2: 67%                   Z   2.5114
      N: 862         p (1-sided)   0.0060
 Events: 510        ~HR at bound   0.8005
   Month: 25    P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.79   0.5603
       Final                   Z   1.9930
      N: 862         p (1-sided)   0.0231
 Events: 765        ~HR at bound   0.8657
   Month: 60    P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.79   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’s reported primary analysis is the Cox regression hazard ratio of 0.79, with a 90% confidence interval from 0.46 to 1.35 and p = 0.47. This is the sponsor’s own analysis as posted and is the primary basis for describing the registry’s PFS result. The record identifies the analysis as non-inferiority, but does not state the margin or the rule used to reach a conclusion.

Recalculated comparisons are simple, unadjusted calculations from posted summary statistics. They can be useful as checks or as alternate descriptive summaries, but they do not reproduce a Cox model and cannot account for the timing of events or censoring in the same way. For time-to-event outcomes, the sponsor’s reported hazard ratio takes precedence over a recalculated comparison based only on arm-level summaries. There is no discrepancy flagged for the primary result, but the methods and target estimand still differ between a model-based hazard ratio and an unadjusted summary.

The same distinction applies to secondary outcomes. A recalculated risk difference for a binary endpoint is not the sponsor’s Cox regression or Fisher’s Exact Test. The sponsor’s own reported analyses should be quoted as such, while recalculations should be identified as unadjusted. Neither approach removes the uncertainty associated with the missing multiplicity plan, unspecified missing-data methods, or absent non-inferiority margin.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines multiple outcomes, comparisons, subgroups, or analyses. Without an adjustment or a prespecified testing hierarchy, interpreting each p-value as if it were the only test can make chance findings appear more persuasive. The registry lists several secondary outcomes and multiple analyses, but a multiplicity strategy is not reported in the registry record. It is therefore not possible to determine whether the secondary tests were confirmatory, exploratory, adjusted, or ordered under a formal testing procedure.

The non-inferiority margin is also not reported. This is central to interpreting the primary question: the estimated effect and confidence interval must be evaluated against the prespecified margin and decision rule. The registry’s designation of the primary analysis as non-inferiority does not supply that missing threshold. The original statistical analysis plan and sample-size justification are not reported in the registry record.

The primary PFS population is identified as per protocol, but the criteria for membership are not reported. The registry does not report whether an intention-to-treat analysis was also conducted for PFS, how protocol deviations were handled, or how missing outcome information was treated. It also does not report interim analyses or stopping rules. These absences limit assessment of whether the analysis followed a prespecified plan and how robust the result is to alternative analysis populations.

The outcome timeframe is described as up to 12 months, while the PFS definition gives different starting-point wording in its timeframe and endpoint description. The registry record does not explain this discrepancy. Details about censoring, loss to follow-up, event adjudication, and the number of observed PFS events are also not reported. These are relevant to interpreting time-to-event estimates, but their absence does not justify assuming how they were handled.

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 0% 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 (34.1%), myocardial infarction (2.3%), sepsis (2.3%), abdominal infection (1.2%), acute kidney injury (1.2%).

The registry’s adverse-event fields list 80 participants at risk for serious events in the AryoGen Pharmed group, with 31 affected, and 44 at risk in the Roche group, with 17 affected. For the other adverse-event field, it lists 80 at risk and 75 affected in the AryoGen group, and 44 at risk and 42 affected in the Roche group. The record also lists deaths of 30 and 17, respectively, in these adverse-event group summaries. These are registry counts; they should not be treated as adjusted comparisons or as evidence of causation.

The selected serious-event terms include disease progression at 34.1%, myocardial infarction at 2.3%, sepsis at 2.3%, abdominal infection at 1.2%, acute kidney injury at 1.2%, and gastrointestinal haemorrhage at 1.2%. The record does not clarify in these summaries how the listed percentages relate to unique participants, repeated events, or the listed at-risk groups. The event terms also include disease progression, which is not itself a treatment-related adverse effect by definition.

Because the adverse-event fields have different participant counts from the PFS arm summaries and no adjusted safety analysis is reported, these numbers are descriptive. Timing, severity grading, attribution, exposure duration, and comparative testing details are not reported in the registry record.

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

The posted primary result is an estimate of the relative PFS event rate from a Cox model, accompanied by a 90% confidence interval and a p-value. It is not a direct statement that one product is superior, equivalent, or non-inferior. The interval includes 1 and spans a broad range of possible relative effects under the model. The registry identifies the analysis as non-inferiority, but the necessary margin and decision rule are not reported, so the objective cannot be independently evaluated from the posted result alone.

The arm-specific medians offer descriptive context, but they do not determine the comparative result. They do not show the full event-time distributions, explain censoring, or account for the model structure. The sponsor’s hazard ratio is the appropriate posted comparative summary for PFS; its uncertainty must be considered alongside the absence of key protocol and analysis details.

The secondary analyses give additional outcome-specific information, but they are not a substitute for the primary endpoint. They involve different measures and methods, and the registry does not report a multiplicity plan. Their p-values should therefore not be interpreted as a coordinated confirmatory body of evidence. Likewise, adverse-event counts describe recorded events but do not by themselves establish whether the products differ in safety or whether an event was caused by treatment.

The record does not report the original sample-size assumptions, the non-inferiority margin, interim analyses, missing-data methods, or full analysis populations. These gaps constrain how confidently the findings can be interpreted and reproduced. The record’s inconsistent product naming also requires care: its official title refers to trastuzumab, while the brief summary and arms describe bevacizumab. The conclusion should remain limited to the registry’s posted data and stated comparison, without extending to other populations, regimens, or clinical decisions.

19. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the distinction between a non-inferiority label and evidence that meets a non-inferiority criterion. The registry reports a primary Cox hazard ratio and confidence interval, but does not provide the margin needed to interpret that interval against the trial’s stated objective. A reader can describe the estimate and its precision without claiming that non-inferiority was established.

It also shows why time-to-event results cannot be reduced to arm medians. The PFS medians are descriptive summaries, while the reported comparison uses a Cox regression model that incorporates event timing. Their meanings differ, and the hazard ratio’s uncertainty is central to interpretation. The record’s absent event count, censoring information, and model details further demonstrate why registry summaries may not support full methodological review.

The trial also highlights the importance of separating sponsor analyses from simple unadjusted recalculations. A risk difference from summary counts and a Cox hazard ratio answer different statistical questions. Likewise, secondary outcomes tested without a reported multiplicity strategy should be treated with more caution than a prespecified primary analysis.

Finally, the inconsistent naming in the official title and the treatment descriptions underscores a practical issue in evidence interpretation: even basic trial identity and intervention details need to be checked across record fields. Careful reading preserves what the registry does report while avoiding conclusions that depend on information it does not report.

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 leaves several trial-specific details unresolved. Its official title names AryoGen trastuzumab, while the brief summary and arm descriptions specify AryoGen Pharmed bevacizumab; the title also uses the name Stivant. The exact product identity should therefore be interpreted from the treatment descriptions with caution. The record describes blinding differently across fields: the official title says triple blinded, while the masking field and brief summary say double blinded, with the brief summary naming patients and assessors.

The PFS timeframe says measurement began at chemotherapy start, while the endpoint definition says randomization. The reason for this difference is not reported. The primary population is per protocol, but its criteria are absent, as are details of any intention-to-treat analysis. The record does not report the non-inferiority margin, original sample-size justification, interim analyses, stopping rules, censoring procedures, missing-data handling, or model covariates.

The registry lists enrollment of 126, but the PFS arm summaries contain 72 and 40 participants; it does not explain the difference. Endpoint-specific populations also vary across the posted results, and the record does not provide a complete account of why. PFS event counts and follow-up distributions are not reported, limiting independent assessment of information and precision.

Several secondary outcomes are named, but detailed numerical results are not available for every listed outcome. The record does not describe a multiplicity strategy. Safety summaries do not supply sufficient detail on event attribution, grading, timing, or the relation of percentages to participants and repeated events. These limitations restrict interpretation of both efficacy and safety and should not be filled by assumptions.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Comparing Efficacy and Safety of Stivant (AryoGen Bevacizumab) Versus Avastin in Metastatic Colorectal Cancer — NCT03288987.
• Registry record last updated 2021-01-22; status last verified 2020-09.
• Results first posted 2021-01-22.
• 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 Phase III randomized, parallel active-controlled comparison of AryoGen Pharmed bevacizumab plus FOLFIRI-3 with Roche bevacizumab plus FOLFIRI-3 in metastatic colorectal cancer. Enrollment is listed as 126, with a 2:1 allocation described in the brief summary. The primary endpoint is PFS in a per-protocol population.

The sponsor reports a Cox hazard ratio of 0.79 for PFS, with a 90% confidence interval from 0.46 to 1.35 and p = 0.47. The analysis is labeled non-inferiority, but the margin and decision rule are not reported in the registry record. The record also contains selected secondary and safety results, with differing methods and analysis populations.

Interpretation is limited by missing design and analysis details, including the original sample-size justification, multiplicity plan, missing-data procedures, and PFS event information. The record also contains inconsistencies in intervention naming and blinding descriptions. The posted statistics describe the registry results but do not, by themselves, establish non-inferiority or resolve the uncertainty around the PFS comparison.