Review Reports - Real-World Emulation of Landmark Lung Cancer Trials: A Registry-Based Reconstruction of KN189, KN407, IMpower133, and PACIFIC

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Thank you for the opportunity to review this manuscript entitled: Real-World Emulation of Landmark Lung Cancer Trials: A Registry-Based Reconstruction of KN189, KN407, IMpower133, and PACIFIC.

The manuscript addresses whether the efficacy in randomized controlled trials gives the same effectiveness in the real-world population. This article has a very interesting topic because it is a bridge between internal legitimacy and clinical everyday life.

The study’s main strength is that, because of the utility of the Baden-Württemberg Cancer Registry (BWCR), the study provides a very large sample size of 40000 patients. Also, it is very positive that you aligned the eligibility criteria, time-zero, and treatment strategies with the original trials, since it reduces observational biases.

But, there are also limitations regarding the nature of registry data, such as the lack of detailed data and smoking status.

Overall, the manuscript is very useful for the whole oncology community. It shows how high-quality registries can enhance RCT evidence.

Simple summary & Abstract

Lines 16-27

The simple summary is well-written and very nicely summarizes the overall scope of the study.

Lines 35-36

The term ‘time-zero’ seems undefined. Is it the start of systematic therapy or the end of radiotherapy? Please clarify it, because the abstract is crucial since it’s usually the most read section of manuscripts.

Lines 46-47

Instead of mentioning ‘consistently higher’ it would be better to include the actual percentages to show objective evidence.

Introduction

Lines 84-86

It would be beneficial to mention that the framework you used has previously been applied to German registry data to document the approach's reliability in this context.

Materials and Methods

Lines 127-129

It would be beneficial to discuss whether additional registry markers were used to distinguish between diseases that were unresectable surgically and patients who weren’t going for surgery because of preference or bad performance status.

Lines 135-139

Please give more details about the ‘tumor status’ field. Please mention the frequency with which the oncologist's reports are registered with the BWCR. By this, you would justify the use of the objective response rate as a secondary endpoint even though it does not fully correspond with the RESIST-defined ORR.

Results

Lines 190-192

You should mention how many patients were excluded because the ECOG performance status data were missing. It is important to evaluate attrition bias.

Lines 259-261

Because in the real-world cohort, patients were older, and there was a bigger prevalence of brain metastasis, you should clarify if these factors were adjusted so that HR can be estimated to the point.

Lines 347-349

Except for the median radiation dose, it would be better to mention also the range of the radiation doses that were registered in the ePACIFIC cohort study. Because the variance in the final radiation dosage in everyday clinical practice may influence the effectiveness of durvalumab.

Discussion

Lines 406-407

Even though a durable benefit is shown across all cohorts through the exhibited ‘plateau’, it would be impactful if you could clarify whether there were some basic characteristics of the long-term survivors that are different from those that are registered to the original RCTs.

Lines 428-435

It is essential the clarification for the fact that whether the shown advantage that cisplatin has is because of drug efficacy or the patient selection, regardless of the propensity score weighting.

Tables

Overall, the tables are well-arranged and informative.

Author Response

Response 0: We thank the reviewer for the positive feedback and helpful suggestions, which have strengthened the manuscript.

Simple summary & Abstract

Lines 35-36

Response1: Thank you. We have clarified in the Abstract that time zero was defined as treatment initiation for systemic therapy cohorts (eKN189, eKN407, eIMP133) and as the end of radiotherapy for ePACIFIC.

Lines 46-47

Instead of mentioning ‘consistently higher’ it would be better to include the actual percentages to show objective evidence.

Response2: Thank you. We revised the Abstract to include objective response rates and survival percentages for all cohorts.

Introduction

Lines 84-86

It would be beneficial to mention that the framework you used has previously been applied to German registry data to document the approach's reliability in this context.

Response3: We thank the reviewer for this helpful suggestion. We agree that target trial emulation has previously been applied in population-based cancer registry data to assess real-world treatment effects and approximate randomized controlled trial results. We have added a statement in the Methods/Discussion section to better contextualize our approach, to acknowledge prior applications of this framework in similar real-world data settings, and to expand the discussion of the relevant methodological literature.

Materials and Methods

Lines 127-129

Response4: We have clarified that unresectability was operationalized based on absence of tumor-specific surgery codes. We acknowledge that registry data do not allow full distinction between technically unresectable disease, medical inoperability, or patient preference, and now discuss this as a limitation.

Lines 135-139

Response5: Additional details on the tumor status field and reporting structure of the BWCR have been added to the Methods. We now clarify that tumor response assessments are derived from routine oncologic follow-up reports and therefore represent clinically documented responses rather than RECIST-based centralized assessments.

Results

Lines 190-192

You should mention how many patients were excluded because the ECOG performance status data were missing. It is important to evaluate attrition bias.

Response6: We agree and now report the number of patients excluded due to missing ECOG performance status in the Figure 1.

Lines 259-261

Response7: Thank you. Age and presence of brain metastases were included as baseline covariates in the propensity score model. This is now explicitly stated in the Methods and referenced in the corresponding Results sections.

Lines 347-349

Response8: We have added the observed range of radiation doses in the ePACIFIC cohort to the Results section.

Discussion

Lines 406-407

Response9: We agree this is an interesting question. However, a dedicated analysis of long-term survivor characteristics was beyond the scope of the present study, which focused on trial emulation and reproducibility of trial-level outcomes. This point is now acknowledged in the Discussion as an area for future research.

Lines 428-435

It is essential the clarification for the fact that whether the shown advantage that cisplatin has is because of drug efficacy or the patient selection, regardless of the propensity score weighting.

Response10: We agree and have expanded the Discussion to emphasize that observed differences between cisplatin- and carboplatin-based regimens may reflect both treatment-related effects and residual patient selection, despite propensity score weighting. These subgroup findings should therefore be interpreted cautiously.

Tables

Overall, the tables are well-arranged and informative.

Reviewer 2 Report

Comments and Suggestions for Authors

The authors provided an interesting statistical analysis comparing RWE and RCTs.

Please take into consideration my comments:

This is clearly just a statistical analysis, because when you matched the exact same patient’s characteristics and you have enough large numbers, the results must be more or less the same.
The real challenge is to produce the same results from RCTs in heavily-pretreated, high tumor burden cancer patients, from real life clinical practice, who are usually excluded from RCTs.
From my clinical oncological perspective comparing the same populations, the authors did not succeed in translating RCTs results in clinical practice.
This is an interesting statistical analysis, but the authors must discuss further the implications for clinical relevance. According to national restrictions and reimbursement’s regulations, oncologists respect protocols, that match inclusion and exclusion criteria from RCTs. It is common sense that perfectly matched cancer cohorts would have the same results. The mentioned RCTs have solid data and results and a reconfirmation would be challenging just in real life cancer patients, and the authors missed to prove exactly this.
I do not identify the relevance of this statistical analysis for the medical audience. Please explain.

Author Response

Comments and Suggestions for Authors

The authors provided an interesting statistical analysis comparing RWE and RCTs.
Please take into consideration my comments:

Response1: We thank the reviewer for the thoughtful comments and for highlighting the importance of clarifying the clinical relevance of our work.

Our study was intentionally designed as a target trial emulation, aiming to assess whether the efficacy estimates observed in landmark randomized controlled trials (RCTs) can be reproduced using high-quality population-based real-world data under trial-like conditions. The primary objective was therefore not to investigate treatment effects in broader or heavily pretreated populations, but rather to evaluate the transportability and reproducibility of RCT findings in routine care using observational data.

This is clearly just a statistical analysis, because when you matched the exact same patient’s characteristics and you have enough large numbers, the results must be more or less the same.

Response 2: We agree that restricting analyses to patients approximating the original trial eligibility criteria increases comparability with the corresponding RCTs. However, reproducing trial-level estimates using observational registry data remains methodologically challenging due to treatment-selection bias, immortal time bias, non-random treatment allocation, and differences in treatment implementation and follow-up.

The purpose of this study was therefore not simply descriptive matching, but formal emulation of landmark RCTs using explicit specification of eligibility criteria, treatment strategies, time zero, follow-up, and endpoints within a target trial framework. We have clarified this objective in the revised Introduction and Discussion.

The real challenge is to produce the same results from RCTs in heavily-pretreated, high tumor burden cancer patients, from real life clinical practice, who are usually excluded from RCTs.

Response 3: We agree that extending these analyses to broader and less selected patient populations is highly relevant. However, the primary aim of the present study was first to evaluate whether landmark immunotherapy trial findings can be approximated in routine-care patients aligned with the original trial eligibility criteria. We now emphasize more clearly that our conclusions relate to the transportability of RCT findings to comparable routine-care populations, while analyses in broader real-world cohorts remain an important area for future research.

From my clinical oncological perspective comparing the same populations, the authors did not succeed in translating RCTs results in clinical practice.

Response 4: We respectfully disagree. Translation into clinical practice does not necessarily require inclusion of entirely unselected patient populations, but also includes evaluating whether treatment effects observed under randomized conditions remain observable under routine care delivery, documentation, and follow-up. To avoid overstatement, we revised the manuscript to clarify that our study evaluates the transportability of RCT findings to routine-care patients approximating trial eligibility criteria rather than all-comer populations.

This is an interesting statistical analysis, but the authors must discuss further the implications for clinical relevance. According to national restrictions and reimbursement’s regulations, oncologists respect protocols, that match inclusion and exclusion criteria from RCTs. It is common sense that perfectly matched cancer cohorts would have the same results. The mentioned RCTs have solid data and results and a reconfirmation would be challenging just in real life cancer patients, and the authors missed to prove exactly this.

Response 5: We have expanded the clinical implications in the revised Discussion. Specifically, we now emphasize that registry-based trial emulation can:

assess transportability of pivotal trial findings,
complement RCT evidence under routine care conditions, and
support evidence generation where new randomized studies may not be feasible.

We believe this is directly relevant to oncologists implementing immunotherapy regimens in daily practice.

I do not identify the relevance of this statistical analysis for the medical audience. Please explain.

Response 6: We have strengthened the clinical framing throughout the manuscript.

The clinical relevance lies in demonstrating that checkpoint inhibitor–based strategies achieve outcomes in routine practice broadly consistent with pivotal trials when applied to comparable patient populations. This provides reassurance regarding the implementation of these regimens in daily oncology care and illustrates how registries may support evidence generation beyond traditional trials.

Reviewer 3 Report

Comments and Suggestions for Authors

A clear explanation of the explicit specification of the hypothetical target trial protocol for each emulation should be provided. A structured table summarizing how each emulated trial aligns with the original RCT would improve clarity. The degree of deviation from original trials should also be described along with the alignment. Unmeasured confounding (e.g., PD-L1 status completeness, comorbidities, socioeconomic factors) needs to be discussed. Sensitivity analyses (e.g., E-values, negative controls, or alternative weighting approaches) are missing. Conditional exchangeability is assumed and it should be clearly discussed and justified. A section should be added to discuss the missingness mechanism (MCAR/MAR/MNAR) and about imputation strategy. Inclusion criteria restrict patients to ECOG 0–1, which corresponds to trials but limits the representation of real world scenarios. It is warranted to discuss how this selection may overestimate treatment effects and Clarify exclusion proportions (e.g., Figure 1 shows large exclusions due to ECOG/missing data). The authors should describe how response assessments were harmonized and discuss potential misclassification bias compared to RCTs. As the manuscript combines results from four biologically and clinically distinct settings, it is recommended that more nuanced interpretation per disease context should be added and should avoid overgeneralization of ICI effectiveness across all setting. A statement should be added that subgroup analyses are hypothesis-generating only. Authors should discuss external validity limitations. For figures and tables, table captions should be more descriptive. Improve the readability of Kaplan-meier curves on pages 8, 10, 12, 14. Consistent use of CPI vs ICI and CTx vs CITx should be used. Define all abbreviations at first use.

Author Response

Comments and Suggestions for Authors

Response 0: We thank the reviewer for the constructive and methodologically focused comments. We have revised the manuscript substantially to improve transparency of the target trial emulation framework, clarify assumptions, and better discuss limitations related to residual confounding, missing data, and external validity.

A clear explanation of the explicit specification of the hypothetical target trial protocol for each emulation should be provided. A structured table summarizing how each emulated trial aligns with the original RCT would improve clarity.

Response 1: We agree and have added a dedicated supplementary table summarizing, for each emulated trial, the alignment with the original RCT regarding:

eligibility criteria,
treatment strategies,
time zero,
follow-up,
endpoints,
analytic approach.

We additionally report key deviations imposed by registry data availability (e.g., absence of RECIST-based response assessment, incomplete biomarker data, and operationalization of unresectability in ePACIFIC).

The degree of deviation from original trials should also be described along with the alignment.

Response 2: This has now been explicitly incorporated into both the Methods and Discussion. We clarify that eligibility criteria were operationalized using available registry variables and therefore represent clinically meaningful approximations rather than exact protocol replication.

Unmeasured confounding (e.g., PD-L1 status completeness, comorbidities, socioeconomic factors) needs to be discussed.

Response 3: We expanded the limitations section to explicitly discuss residual confounding from incompletely captured or unavailable variables, including:

incomplete PD-L1 reporting,
lack of systematic smoking/comorbidity data,
absence of socioeconomic variables.

We now explicitly state that conditional exchangeability is assumed but cannot be fully verified.

Sensitivity analyses (e.g., E-values, negative controls, or alternative weighting approaches) are missing.

Response 4: We acknowledge that additional sensitivity analyses may further strengthen causal interpretation. Our primary objective was faithful emulation of landmark RCTs using a consistent framework across four cohorts. IPTW was selected a priori because it preserves the full eligible population and targets the marginal treatment contrast most analogous to randomized comparisons. We now discuss absence of additional sensitivity analyses as a limitation and highlight this as future work.

Conditional exchangeability is assumed and it should be clearly discussed and justified.

Response 5: We expanded the Methods and Discussion to explicitly state that weighted estimates rely on assumptions of:

conditional exchangeability,
positivity,
correct model specification.

We additionally discuss that, although major measured prognostic variables were included, unmeasured confounding cannot be excluded.

A section should be added to discuss the missingness mechanism (MCAR/MAR/MNAR) and about imputation strategy.

Response 6: We added a dedicated missing data section in Methods. Patients with missing ECOG status were excluded because ECOG 0-1 was part of trial eligibility emulation. PD-L1 subgroup analyses were restricted to available cases only. No formal multiple imputation was performed, as missingness was variable-specific and often structurally related to routine clinical documentation rather than plausibly missing completely at random. This limitation is now discussed.

Inclusion criteria restrict patients to ECOG 0–1, which corresponds to trials but limits the representation of real world scenarios.

Response 7: Because the study objective was target trial emulation rather than all-comer effectiveness analysis, restriction to ECOG 0-1 was necessary to align with the original RCT populations. We now explicitly discuss that this may overestimate treatment effects relative to broader real-world populations and limits generalizability beyond trial-eligible patients.

It is warranted to discuss how this selection may overestimate treatment effects and Clarify exclusion proportions (e.g., Figure 1 shows large exclusions due to ECOG/missing data).

Response 8: We now report the number of excluded patients due to:

ECOG >1,
missing ECOG,
non-protocol systemic treatment.

These details were added to Figure 1.

The authors should describe how response assessments were harmonized and discuss potential misclassification bias compared to RCTs.

Response 9: We expanded the Methods to describe the registry “tumor status” field in more detail. Tumor response was derived from routine clinical update reports and categorized as complete remission, partial remission, stable disease, or progression. We explicitly acknowledge that this does not fully correspond to RECIST-based centralized response assessment and may introduce misclassification bias.

As the manuscript combines results from four biologically and clinically distinct settings, it is recommended that more nuanced interpretation per disease context should be added and should avoid overgeneralization of ICI effectiveness across all setting.

Response 10: We agree and revised the Discussion to avoid overgeneralization. Interpretation is now more explicitly contextualized separately for:

metastatic non-squamous NSCLC,
metastatic squamous NSCLC,
ES-SCLC,
unresectable stage III NSCLC.

We now frame conclusions as reproducibility of trial findings within specific clinical settings rather than universal ICI effectiveness.

A statement should be added that subgroup analyses are hypothesis-generating only.

Response 11: We agree and now explicitly state that all subgroup analyses are exploratory and hypothesis-generating.

Authors should discuss external validity limitations.

Response 12: We strengthened discussion of external validity, emphasizing that conclusions apply primarily to routine-care patients approximating trial eligibility criteria and not fully unselected populations.

For figures and tables, table captions should be more descriptive. Improve the readability of Kaplan-meier curves on pages 8, 10, 12, 14. Consistent use of CPI vs ICI and CTx vs CITx should be used. Define all abbreviations at first use.

Response 13: We revised table captions to be more descriptive, improved readability of Kaplan–Meier curves, standardized terminology throughout the manuscript (ICI, CTx), and ensured all abbreviations are defined at first use.

Reviewer 4 Report

Comments and Suggestions for Authors

Major revision recommendation

The manuscript addresses a clinically relevant topic; however, substantial methodological and interpretative concerns currently limit its suitability for publication. Although the target trial emulation framework is ambitious, the manuscript insufficiently addresses residual confounding, missing data handling, treatment-selection bias, and temporal heterogeneity across cohorts. The propensity score methodology lacks adequate sensitivity analyses and calibration diagnostics. Several subgroup conclusions appear overstated given limited statistical power and absence of multiplicity adjustment. Moreover, the discussion underemphasizes important discrepancies between registry-derived populations and the original RCT cohorts, weakening claims regarding external validity and causal reproducibility.

Why did the authors choose IPTW alone without performing sensitivity analyses using overlap weighting, matching, or doubly robust estimation to assess robustness of treatment effects?
The manuscript interprets weighted analyses as “intention-to-treat-like,” yet treatment switching, discontinuation, and crossover are not described. How can an ITT-like interpretation be defended without longitudinal treatment adherence data?
The eKN189 cohort demonstrates substantially higher rates of brain metastases compared with the original KEYNOTE-189 trial (33% vs 17%). Could this discrepancy fundamentally alter comparability and external validity of the emulation?
The manuscript does not report missing data proportions for key variables. How much data were missing for ECOG, PD-L1 expression, metastatic sites, and response assessments, and how were these missing values handled analytically?
In the eKN407 cohort, the chemotherapy-only arm is relatively small (n=91). How do the authors exclude instability of hazard ratio estimates and positivity violations in the IPTW model?
The authors claim “good comparability” after weighting based solely on SMD <0.1. Why were graphical balance diagnostics and variance ratio assessments not presented?
PD-L1 subgroup analyses are presented, but the manuscript does not specify assay methods, completeness of PD-L1 testing, or harmonization across centers. How reliable are these subgroup findings?
Why were molecularly defined NSCLC subgroups (EGFR, ALK, ROS1, etc.) not explicitly excluded or analyzed separately, especially given differing immunotherapy responsiveness?

Author Response

The manuscript addresses a clinically relevant topic; however, substantial methodological and interpretative concerns currently limit its suitability for publication. Although the target trial emulation framework is ambitious, the manuscript insufficiently addresses residual confounding, missing data handling, treatment-selection bias, and temporal heterogeneity across cohorts. The propensity score methodology lacks adequate sensitivity analyses and calibration diagnostics. Several subgroup conclusions appear overstated given limited statistical power and absence of multiplicity adjustment. Moreover, the discussion underemphasizes important discrepancies between registry-derived populations and the original RCT cohorts, weakening claims regarding external validity and causal reproducibility.

Response 1: We thank the reviewer for the thoughtful and methodologically rigorous comments. We have revised the manuscript accordingly and expanded the Methods, Results, and Discussion to better clarify the assumptions and limitations of our target trial emulation framework.

We believe these revisions substantially strengthen the methodological transparency of the manuscript and clarify the scope and interpretation of our target trial emulation analyses.

Why did the authors choose IPTW alone without performing sensitivity analyses using overlap weighting, matching, or doubly robust estimation to assess robustness of treatment effects?

Response 2: We thank the reviewer for this important comment. IPTW was selected because our objective was to emulate the marginal treatment contrast of the corresponding randomized trials while preserving the full eligible study population.

Matching would have reduced sample size and altered the target population, whereas overlap weighting targets a different estimand focused on patients with maximal covariate overlap. We therefore considered IPTW most aligned with the objective of target trial emulation.

The manuscript interprets weighted analyses as “intention-to-treat-like,” yet treatment switching, discontinuation, and crossover are not described. How can an ITT-like interpretation be defended without longitudinal treatment adherence data?

Response 3: We agree and revised the manuscript accordingly.

The term “intention-to-treat-like” has been removed. Weighted analyses are now described as estimates of baseline treatment strategy effects conditional on treatment assignment at time zero. We additionally discuss lack of longitudinal treatment adherence, discontinuation, and crossover information as a limitation.

The eKN189 cohort demonstrates substantially higher rates of brain metastases compared with the original KEYNOTE-189 trial (33% vs 17%). Could this discrepancy fundamentally alter comparability and external validity of the emulation?

Response 4: We agree this difference is clinically relevant.

Brain metastases were included as baseline covariates in the propensity score model. We now discuss this discrepancy more explicitly in Results and Discussion as a limitation for direct comparability, while noting that treatment effects remained broadly consistent despite broader routine-care characteristics.

The manuscript does not report missing data proportions for key variables. How much data were missing for ECOG, PD-L1 expression, metastatic sites, and response assessments, and how were these missing values handled analytically?

Response 5: We have added a dedicated paragraph on missing data handling in the Methods.

Patients with missing ECOG status were excluded due to eligibility requirements. PD-L1 subgroup analyses were restricted to patients with available results, and response analyses were limited to patients with documented follow-up.

Missingness for key variables is now explicitly reported.

In the eKN407 cohort, the chemotherapy-only arm is relatively small (n=91). How do the authors exclude instability of hazard ratio estimates and positivity violations in the IPTW model?

Response 6: We acknowledge the limited size of the chemotherapy-only arm.

However, post-weighting balance remained acceptable (all SMD <0.1), and overlap between treatment groups was considered adequate. We now explicitly acknowledge reduced precision and possible instability of subgroup estimates in smaller strata.

The authors claim “good comparability” after weighting based solely on SMD <0.1. Why were graphical balance diagnostics and variance ratio assessments not presented?

Response 7: We agree and have added Love plots demonstrating covariate balance before and after weighting to the Supplementary Material.

PD-L1 subgroup analyses are presented, but the manuscript does not specify assay methods, completeness of PD-L1 testing, or harmonization across centers. How reliable are these subgroup findings?

Response 8: We now clarify that PD-L1 testing was performed as part of routine care, was incomplete, and not harmonized across centers or years. Assay information was not uniformly available.

PD-L1 subgroup analyses are now explicitly described as exploratory.

Why were molecularly defined NSCLC subgroups (EGFR, ALK, ROS1, etc.) not explicitly excluded or analyzed separately, especially given differing immunotherapy responsiveness?

Response 9: Molecular testing variables were incompletely available in the registry across the study period and could therefore not be reliably incorporated as exclusion criteria.

However, because the included treatment regimens reflect first-line immunotherapy-based protocols used in routine practice and aligned with the emulated trial populations, the proportion of actionable oncogene-driven tumors receiving these regimens is expected to be low.

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

I appreciate the authors effort to thoroughly revise the manuscript.

All my comments have been answered.

Form my point of view, the revised version of the article is ready to be published.