Study of IBI308 With Advanced/Metastatic Esophageal Squamous Cell Carcinoma After Failure of First-line Treatment: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of IBI308 With Advanced/Metastatic Esophageal Squamous Cell Carcinoma After Failure of First-line Treatment (NCT03116152), a randomized phase 2 study. The primary outcome is Overall Survival.

2. Clinical Question

The trial addressed a treatment-comparison question in a defined clinical setting: advanced or metastatic esophageal squamous cell carcinoma following failure of first-line treatment. The study compared IBI308 with a chemotherapy regimen containing paclitaxel and irinotecan. Its primary endpoint was overall survival, a time-to-event outcome that follows participants from randomization until death from any cause. The registry record also lists progression-free survival, objective response rate, and duration of response as secondary outcomes.

The main comparative statistic is the hazard ratio reported by the sponsor using a Log Rank analysis. It expresses the relative event rate over follow-up under the analysis assumptions; it is not a ratio of the two median survival times. The group medians and their confidence intervals provide a complementary description of the observed survival distributions. Neither statistic alone describes every participant’s course or establishes why an outcome occurred.

The study was randomized and open-label. Randomization supports a comparison between assigned groups, while the absence of masking means participants and study staff knew the assigned treatment. The registry record does not report details such as the randomization procedure or safeguards used for particular outcome assessments. The results therefore need to be read as estimates from this specific trial and analysis population, rather than as a complete account of every clinical consideration.

3. Trial Design

ORIENT-2 was a randomized, open-label, multicenter, parallel-group phase 2 study. It enrolled 190 participants with advanced or metastatic esophageal squamous cell carcinoma after failure of first-line treatment. The registry record lists 95 participants in each efficacy group. It identifies the study as completed, with a start date of 2017-05-10 and primary completion on 2019-10-02.

The intervention was IBI308, called sintilimab in the reported arms. The listed regimen was 200mg by intravenous drip every three weeks. The comparator was paclitaxel/irinotecan: paclitaxel 175mg/㎡ by intravenous drip every three weeks and irinotecan 180mg/㎡ by intravenous drip every two weeks. The study was not masked. The registry record describes a parallel-group comparison, rather than a design in which participants switch between treatments.

The primary endpoint was overall survival. The registry defines it as time from randomization to death due to any cause and reports the median with a 95% confidence interval. The stated timeframe is through the final analysis data cutoff date of 2-August-2019, up to approximately 26 months. The efficacy analysis population consisted of all randomized participants. This description identifies the population used for efficacy analysis; it does not establish that every randomized participant had complete follow-up or outcome information.

Progression-free survival, objective response rate, and duration of response were listed as secondary outcomes. The registry record reports analyses for progression-free survival and objective response rate, but a result for duration of response is not reported in the registry record. Detailed eligibility criteria, the original sample-size justification, allocation procedures, treatment discontinuation rules, and the protocol’s full statistical analysis plan are not reported in the registry record. The planning illustrations based on observed effects should not be mistaken for the design assumptions used when the trial was planned.

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: 253 enrolled. 190 randomized. Non-randomized reasons: 55 no longer met study criteria, 4 withdrew consent, 4 other. 181 treated (94 sintilimab, 87 chemotherapy).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The efficacy analysis population consisted of 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: All randomized participants

6. Primary Endpoint

The registry lists the primary outcome as Overall Survival, measured over Through Final Analysis data cutoff date of 2-August-2019 (up to approximately 26 months).

Overall survival measures the time from randomization until death from any cause. The registry reports this endpoint as a median time in months for each group, together with a 95% confidence interval, and defines the analysis period as through the final analysis data cutoff date of 2-August-2019, up to approximately 26 months.

A time-to-event endpoint uses both whether an event occurred and when it occurred. Participants whose deaths have not been observed by the cutoff may contribute follow-up information up to their last recorded time without being treated as if they had died. The registry record does not describe the handling of censoring or missing survival information in detail. In general, survival methods are useful when follow-up times differ and some event times are not observed during the analysis period.

The median is the time by which half of the relevant survival distribution has experienced the event, under the survival estimate used. It offers an interpretable summary of follow-up, but it does not capture the entire survival curve. The hazard ratio reported for the comparison instead summarizes relative event rates over follow-up under its statistical assumptions. It is not interchangeable with a difference between medians, and it does not state how long any individual participant lived.

Overall survival is used because it concerns death from any cause rather than a measure that depends on judging disease progression or tumor response. That makes its event definition comparatively direct, though follow-up and analysis choices still matter. The registry’s endpoint definition does not by itself explain the completeness of follow-up, censoring decisions, or any sensitivity analyses.

7. Results Posted in the Registry

• Sintilimab vs Chemotherapy: hazard ratio 0.70 (95% CI 0.50–0.97), reported p = 0.032 (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

• Endpoint type: Time to event: compared as a hazard ratio.
• Test: Hazard ratio as reported by the sponsor (Log Rank); it was not recalculated.
• Result:
  • Sintilimab vs Chemotherapy: hazard ratio 1.00 (95% CI 0.72–1.39), reported p = 0.979 (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 Sintilimab vs Chemotherapy and the control. The interval gives the range of effects that remain compatible with the data.

Objective Response Rate

• 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:
  • Chemotherapy: 6.3% (6/95) versus 12.6% (12/95) on control; risk difference -6.3 percentage points (95% CI -14.6 to 2.0), risk ratio 0.50 (0.20–1.28); unadjusted two-proportion z-test p = 0.137.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Chemotherapy and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add context but do not replace the primary overall-survival comparison. Progression-free survival concerns a different point in the disease course and is analyzed as a time-to-event outcome. Objective response rate is a binary summary of response. Duration of response is listed among the secondary outcomes, but a result is not reported in the registry record. Because the endpoints capture different events and use different summaries, their estimates need not move in the same direction or carry the same precision.

Across the posted secondary results, progression-free survival does not show a clear comparative separation in the sponsor-reported analysis, while the objective-response estimates are accompanied by uncertainty that includes no difference in the sponsor-reported interval. These findings do not erase or confirm the overall-survival result: each outcome addresses a separate question and has its own analysis and measurement considerations. The registry record does not provide a complete account of assessment schedules, missing assessments, or endpoint-specific sensitivity analyses.

Secondary analyses generally carry less weight when many outcomes or comparisons are examined without a reported adjustment for multiplicity. Testing multiple hypotheses increases the chance that at least one result appears unusual by chance. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Thus, secondary results are best read as supportive or exploratory evidence, with attention to their uncertainty, rather than as independent confirmations of the primary finding.

The registry lists four outcome measures and reports analyses for overall survival, progression-free survival, and objective response rate. A duration-of-response result is not reported in the registry record. The absence of a posted result does not establish why it is absent or whether the outcome was not measured; that explanation is not reported in the registry record.

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

• Progression-free Survival
• Objective Response Rate
• Duration of Response

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is time-to-event data: each participant contributes information about the time from randomization to death or, if death has not been observed during follow-up, to the last time that can be used in the analysis. General survival methods can include such censored follow-up rather than discarding participants who have not had the event by the cutoff. The registry record defines overall survival and gives the cutoff period, but detailed censoring rules and checks of those rules are not reported in the registry record.

What does a median survival time describe?

A median is a summary of the estimated survival distribution, marking the time at which the estimated proportion still alive reaches the halfway point. It is not the mean survival time and does not show the shape of the full survival curve. A median can be estimated even when some participants are censored, depending on the observed follow-up and the method used. The registry gives group medians and confidence intervals, but does not provide enough detail to reconstruct the full curves or evaluate the method’s diagnostics.

How should the hazard ratio be read?

The reported hazard ratio compares the event rate between groups over the observed follow-up, according to the sponsor’s analysis. A value below 1 indicates a lower estimated hazard in the first-named group relative to the second-named group under that comparison; a value near 1 indicates little estimated relative difference. It is not the ratio of the two medians, nor does it directly give the probability that a participant survives to a particular time.

A hazard ratio is often interpreted as a single summary across follow-up. That summary can be harder to interpret if the relative event rates change over time. The registry record reports the hazard ratio and Log Rank method but does not report a proportional-hazards assessment, time-varying effects, or an alternative model. Therefore, the reported statistic should be understood as the sponsor’s chosen summary, not as evidence that its assumptions were tested or confirmed.

What does the Log Rank method contribute?

In general, a Log Rank test compares the event experience of groups over follow-up, taking account of the timing of events and censored observations. The registry identifies Log Rank as the method for the overall-survival comparison and reports a hazard ratio with a 95% confidence interval and p-value. The record does not state all details of how the hazard ratio was estimated alongside the test, nor whether any stratification or covariate adjustment was used. Those details are not reported in the registry record.

How do confidence intervals and p-values differ?

A confidence interval describes the uncertainty around an estimate under the analysis method. The interval for a hazard ratio gives a range of values compatible with the data and assumptions at the stated confidence level; it is not a range of individual participant outcomes. A p-value assesses how unusual the observed test statistic would be under a specified null hypothesis and model. It does not measure the probability that the null hypothesis is true, nor does it measure clinical importance. Both statistics depend on the analysis and the data; neither removes uncertainty about design or conduct.

For objective response rate, the outcome is binary: participants are categorized according to whether a response was observed under the outcome definition. The registry posts group percentages and a sponsor-reported difference in percentages with a confidence interval. The recalculated comparison is an unadjusted calculation from posted summary statistics and should not be treated as identical to a protocol-specified model. The response criteria, assessment schedule, and handling of missing response assessments are not reported in the registry record.

The sample-size illustrations use the observed effect as a planning reference, with the effect reduced to stated fractions for alternative scenarios. For time-to-event outcomes, the illustration is expressed as total events and uses the Schoenfeld approach. For other outcomes, it is expressed as participants per arm. The stated planning assumptions are two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation. These are assumptions for the illustrations, not evidence about the trial’s original design calculations. The original sample-size justification and design assumptions are not reported in the registry record.

General statistical interpretation also distinguishes an analysis plan from an analysis that can be reconstructed from posted summary results. The registry identifies the efficacy analysis population as all randomized participants, but it does not report a complete analysis plan, the treatment of protocol deviations, missing-data methods, or sensitivity analyses. Those omissions limit independent evaluation of the robustness of the reported estimates.

11. Confidence Intervals and Precision

The overall-survival hazard ratio is 0.701, with a 95% confidence interval from 0.504 to 0.972. This interval indicates uncertainty around the estimated relative event rate, while also remaining below 1. It is not a guarantee that the underlying value lies within those endpoints, nor does it describe variation in outcomes among individual participants. The reported p-value is 0.032, from the Log Rank analysis.

The median estimate for sintilimab is 7.23 months, with a 95% confidence interval from 5.82 to 9.69. For chemotherapy, the median is 6.21 months, with a 95% confidence interval from 5.39 to 7.85. These intervals describe uncertainty in the group medians. They should not be used as a substitute for the interval around the comparative hazard ratio, since the statistics answer different questions.

Precision is affected by the amount and timing of observed information, including the number of events and the length and completeness of follow-up. The registry states an analysis cutoff through 2-August-2019, up to approximately 26 months, but detailed follow-up distributions and censoring information are not reported in the registry record. The confidence intervals are therefore important alongside the point estimates: they show that the estimates remain uncertain even though the primary comparison is reported as statistically significant.

In general, a narrower confidence interval indicates greater statistical precision than a wider one, all else equal. Precision is distinct from clinical importance and from freedom from bias. A result can be estimated relatively precisely while still depending on the design, measurement, analysis choices, and population studied. The posted confidence intervals do not resolve limitations arising from the open-label design or missing reporting details.

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 illustrations translate observed effects into hypothetical sample-size requirements under stated assumptions. For overall survival and progression-free survival, the figures are total events, not participants per arm. For objective response rate, the figures are participants per arm. The distinction matters because a time-to-event study’s information depends strongly on event accumulation, whereas a binary-outcome calculation is expressed as the number of participants assigned to each group.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario uses a stated fraction of the observed effect. The time-to-event illustrations use the Schoenfeld approach. For each target power, the 80% column means the hypothetical event or participant count needed to have an 80% chance of detecting the specified effect under those assumptions; the 90% column uses a higher target chance of detection. These are planning concepts, not guarantees that a study will detect an effect.

Rows describing planning for 100%, 75%, and 50% of the observed effect illustrate how requirements change if the effect to detect is smaller than the observed estimate. A smaller effect generally requires more information to distinguish it from no difference at the same significance level and target power. The very large event requirements in the progression-free survival illustration reflect the observed hazard ratio’s proximity to 1 under this calculation; they should not be read as a recommendation or as a feasible design for this trial.

These values are planning illustrations based on observed results, not the original trial design calculations. The trial’s own sample-size justification and original assumptions are not reported in the registry record. This is not observed power: it does not measure the probability that the completed trial “had power” after seeing its results, and it should not be used to reinterpret the p-value.

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 = 0.701, so ln(HR) = -0.3552.
2. d = 4 × (1.96 + 0.842)² / [ln(0.701)]² = 248.8, rounded up to 249 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 <- 0.701                              # 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(3116152)
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 = 249 (80% power), 334 (90% power)
 75% of observed effect: events = 443 (80% power), 593 (90% power)
 50% of observed effect: events = 996 (80% power), 1,333 (90% power)
Simulated power with 249 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 377 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 190 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 <- 6.21          # control-arm median, months (converted from the posted unit)
hr          <- 0.701          # 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: 246        p (1-sided)   0.0001
 Events: 113       ~HR at bound   0.4960
   Month: 16   P(Cross) if HR=1   0.0001
             P(Cross) if HR=0.7   0.0338
   IA 2: 67%                  Z   2.5114
      N: 378        p (1-sided)   0.0060
 Events: 225       ~HR at bound   0.7149
   Month: 25   P(Cross) if HR=1   0.0060
             P(Cross) if HR=0.7   0.5603
       Final                  Z   1.9930
      N: 378        p (1-sided)   0.0231
 Events: 337       ~HR at bound   0.8046
   Month: 60   P(Cross) if HR=1   0.0250
             P(Cross) if HR=0.7   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 a sponsor analysis for overall survival using the Log Rank method: hazard ratio 0.701, 95% confidence interval 0.504 to 0.972, and p = 0.032. The posted recalculation does not flag a discrepancy for this result. The sponsor’s reported analysis is the trial’s own comparative result and is the primary reference for interpreting the trial’s conclusion.

For progression-free survival, the sponsor reports a hazard ratio of 1.002, with a 95% confidence interval from 0.722 to 1.391 and p = 0.979. For objective response rate, the sponsor reports a difference in percentages of 6.3, with a 95% confidence interval from -2.2 to 15.4; a sponsor-reported p-value is not present in the registry record. The recalculated unadjusted objective-response comparison gives p = 0.137, based on the posted summary statistics. That calculation is a separate, unadjusted check, not a replacement for an analysis specified by the sponsor.

In general, recalculation from summary statistics cannot reproduce methods that require participant-level records, stratification variables, covariate adjustments, or details of handling missing observations. The registry record does not provide those details. Where sponsor and recalculated results differ, the sponsor’s own analysis takes precedence; the discrepancy flag is false for this record. Recalculations should therefore be read as supplementary checks, not as a competing primary analysis.

16. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several statistical hypotheses are examined. Each additional test creates another opportunity for a result to appear statistically unusual by chance, even if no corresponding effect exists. This is one reason secondary outcomes are usually interpreted with more caution than a designated primary endpoint. The registry record lists progression-free survival, objective response rate, and duration of response as secondary outcomes, but a multiplicity adjustment, testing hierarchy, or other family-wise error procedure is not reported in the registry record.

The primary endpoint is identified as overall survival, and a sponsor-reported analysis is posted for it. The registry record does not report whether interim analyses were conducted, whether alpha was allocated across analyses, or how any interim monitoring would have affected the final analysis. These details are not reported in the registry record and should not be inferred from the final result alone.

The stated efficacy analysis population consisted of all randomized participants. This helps define who was intended to contribute to the efficacy analysis, but the registry record does not describe the handling of participants with missing outcome data, withdrawals, treatment changes, or protocol deviations. It also does not give the number censored at particular times or describe sensitivity analyses for missingness. Those details are not reported in the registry record.

For general interpretation, missing outcome information can matter if the chance of missingness is related to prognosis or treatment experience. Time-to-event methods commonly use censoring, but the validity of an estimate can depend on how censoring relates to the event process. The registry gives the endpoint definition and final-analysis cutoff but does not report enough detail to assess these assumptions. For objective response, missing assessments can affect whether a response is classified as observed, but the relevant rules are not reported in the registry record.

The original protocol, full statistical analysis plan, interim-analysis plan, and detailed missing-data procedures are not reported in the registry record. These are substantive limits on independent evaluation of the analysis, rather than evidence that a particular method was or was not used.

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: bone marrow failure (6.9%), pneumonia (6.4%), pneumonitis (6.4%), upper gastrointestinal haemorrhage (5.3%), lung infection (5.3%).

The registry posts serious adverse event figures for groups with 94 participants at risk in the sintilimab group and 87 at risk in the chemotherapy group. It reports 41 participants affected in the sintilimab group and 23 in the chemotherapy group. The other-adverse-event figures are 88 affected among 94 at risk for sintilimab and 78 affected among 87 at risk for chemotherapy. The registry also reports deaths of 73 and 82, respectively. These are posted counts and should be read with their stated at-risk denominators, not treated as rates calculated on a different denominator.

The registry lists bone marrow failure at 6.9%, pneumonia at 6.4%, pneumonitis at 6.4%, upper gastrointestinal haemorrhage at 5.3%, lung infection at 5.3%, and hepatic function abnormal at 4.3% among the top serious terms. These terms describe reported events; the record excerpt does not establish that each event was caused by assigned treatment. The death counts likewise do not show that deaths were treatment-related. Overall survival counts death from any cause, whereas safety attribution is a separate question.

Adverse-event counts can depend on definitions, observation periods, reporting practices, and whether multiple events in one participant are counted separately. The registry record does not provide the detailed coding, exposure-adjusted analyses, severity breakdown, or causal assessments needed for a fuller comparison. The figures describe the posted safety data, not a complete assessment of benefit and risk.

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

The primary result is a sponsor-reported overall-survival comparison in a randomized phase 2 study of IBI308, identified as sintilimab in the results, versus paclitaxel/irinotecan after first-line treatment failure in advanced or metastatic esophageal squamous cell carcinoma. The reported hazard ratio is 0.701, with a 95% confidence interval from 0.504 to 0.972 and p = 0.032. The group median estimates and their intervals provide additional descriptions of the observed survival data.

Statistically, the reported comparison is evidence of a difference between the assigned groups under the sponsor’s analysis. It does not prove that every participant in one group had a better outcome than every participant in the other. It does not determine the outcome for a particular person, establish the mechanism behind the observed difference, or show that the estimate will hold in other populations or settings. No medical advice follows from these statistics alone.

Overall survival is a measure of time to death from any cause, not a direct measure of symptoms, quality of life, or treatment burden. The registry record does not report those outcomes in the registry record described. Safety counts also require separate interpretation and do not, by themselves, establish causation. The endpoint results and safety reports are complementary, not interchangeable.

The open-label design means treatment assignment was known to participants and study staff. That feature is less directly tied to the definition of death than to outcomes involving clinical assessment or participant reporting, but it remains relevant to trial conduct and interpretation. Detailed information about blinded assessment, follow-up, missing data, and analysis choices is not reported in the registry record. The posted result is therefore best understood as a trial-specific estimate, with uncertainty and reporting limitations, rather than as a complete answer to every question about the treatments.

19. Why This Trial Matters Statistically

ORIENT-2 illustrates how a clinical trial can report several statistical summaries for one primary time-to-event question. Group medians describe the estimated timing of the event within each group; the hazard ratio summarizes the relative event experience over follow-up; and the confidence intervals convey uncertainty around estimates. These quantities answer related but different questions and should not be collapsed into a single number or interpretation.

The trial also demonstrates why the primary endpoint and secondary outcomes need to be kept distinct. Overall survival is the designated primary outcome. Progression-free survival and objective response rate capture other aspects of the disease course, and duration of response is listed without a posted result. Their differing results are not inherently contradictory because the endpoints use different definitions and analysis methods. Multiplicity and the absence of a reported adjustment further counsel against treating each secondary p-value or estimate as an independent confirmatory test.

The sample-size illustrations offer another statistical lesson: planning requirements depend on the effect one intends to detect, the target power, the significance level, allocation assumptions, and the outcome type. For time-to-event comparisons, the illustrations are expressed in total events; for the binary outcome, they are expressed per arm. These retrospective illustrations do not reveal the trial’s original planning rationale.

Finally, a statistically significant primary comparison does not eliminate uncertainty about precision, follow-up, missing information, assumptions, or generalizability. Reading the effect estimate together with its confidence interval, design, analysis population, secondary outcomes, and reporting gaps gives a more balanced understanding than relying on the p-value alone.

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 identifies the study as open-label and reports no masking. Knowledge of treatment assignment can influence aspects of study conduct and assessments, particularly for outcomes that require clinical judgment. Overall survival has a direct event definition, but an open-label design remains part of the context in which all results were generated. The registry record does not report whether any outcome assessment was independently reviewed or blinded.

The reported primary analysis uses a Log Rank method and gives a hazard ratio, but detailed modeling choices and assumption checks are not reported in the registry record. In particular, the record does not describe a proportional-hazards assessment, stratification factors, covariate adjustment, or sensitivity analyses. It also does not provide detailed censoring and follow-up information needed to assess how incomplete observation may have affected the time-to-event estimates.

Although the efficacy analysis population is described as all randomized participants, handling of missing outcome information, protocol deviations, treatment discontinuation, and crossover is not reported in the registry record. The original sample-size justification, interim-analysis procedures, and full statistical analysis plan are also not reported. The sample-size illustrations are based on observed effects and should not be treated as evidence of the planned design.

The registry lists duration of response as a secondary outcome but does not report a result for it. Multiplicity procedures for secondary outcomes are not reported. The posted safety summary does not supply detailed causal attribution or exposure-adjusted analyses. Finally, the trial addresses a specific disease setting and treatment comparison; the registry results alone do not establish how the estimates apply outside that setting.

21. Related Tutorials

22. Related Statistical Calculators

23. Sources

• ClinicalTrials.gov: Study of IBI308 With Advanced/Metastatic Esophageal Squamous Cell Carcinoma After Failure of First-line Treatment — NCT03116152.
• Registry record last updated 2021-02-03; status last verified 2021-01.
• Results first posted 2021-01-19.
• 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

NCT03116152, ORIENT-2, was a randomized, open-label, multicenter, parallel-group phase 2 study of IBI308 versus paclitaxel/irinotecan in advanced or metastatic esophageal squamous cell carcinoma after failure of first-line treatment. The registry lists enrollment of 190 and 95 participants in each efficacy group. The study is marked completed.

The primary endpoint was overall survival, defined as time from randomization to death due to any cause. Through the final analysis data cutoff date of 2-August-2019, up to approximately 26 months, the sponsor reported a Log Rank hazard ratio of 0.701, with a 95% confidence interval from 0.504 to 0.972 and p = 0.032. The efficacy analysis population consisted of all randomized participants.

Progression-free survival and objective response rate were also reported as secondary outcomes. Duration of response was listed, but a result is not reported in the registry record. Detailed analysis-plan, missing-data, multiplicity, and follow-up procedures are not reported in the registry record.