Evidence Mapping of ctDNA Reporting in Pancreatic Ductal Adenocarcinoma: Toward a Shared Quantitative Language for ctDNA

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript argues that the main barrier to quantitative ctDNA use in PDAC is not biology per se but the lack of a shared reference unit. It proposes that, because KRAS truncal mutations are nearly universal in PDAC, reporting KRAS mutant molecules per mL (and deriving KRAS-equivalent units for broader panels) could:

• Harmonise reporting across single-locus and multi-locus assays.
• Distinguish detection from quantification based explicitly on molecule counts.
• Enable more robust cross-study synthesis and clinical interpretation.

From a clinician’s / translational researcher’s viewpoint, this is attractive: it promises a way to interpret very heterogeneous ctDNA outputs in a common language.

Major comments

1. Clinical “use cases” could be more explicitly connected to the framework

The authors correctly note that, in PDAC, ctDNA is most often used for Prognostic stratification (baseline or post-operative), Molecular relapse / MRD detection and Monitoring response in metastatic disease. Wouldn’t the proposed KRAS-based framework would be even more convincing if the author explicitly walked through how it changes decision-making in one or two of these scenarios. For example Post-operative MRD: How would a “detectable but not quantifiable” KRAS result (e.g. 3 molecules in 4 mL plasma) influence adjuvant therapy decisions compared with “not detected”? Could specific KRAS copies/mL thresholds be prospectively tested as “molecular R1 margins” or MRD triggers?

Metastatic disease monitoring: How could a consistent KRAS-based scale help reconcile different ctDNA assays used across centres or countries (e.g. when a patient moves or changes provider)?

My Suggestion to the author would be to include a short “Clinical implications” subsection with 1–2 concrete examples of how using KRAS molecules/mL might alter trial design, clinical reporting, or guideline-level recommendations.

2. Feasibility and adoption barriers

The proposal is intentionally minimal (“does not require changing algorithms”), but in practice, adoption will still require: Assays to explicitly report KRAS copy number and plasma-equivalent volume, which is not always part of the standard report. Commercial vendors to expose sufficient quantitative detail (sometimes they currently provide only a tumour fraction or binary MRD status). Clinicians and Clinical trial studies to agree on at least some shared thresholds and reporting templates.

I would suggest the authors to discuss the practical barriers to implementation and offer suggestions: e.g. reporting KRAS copies/mL as a mandatory field in clinical trial protocols and encouraging regulatory bodies or professional societies to include this in minimum reporting requirements.

3. Integration with existing professional guidance

The authors cited the ASCO/CAP liquid biopsy review and other consensus documents in the background, but it would be useful to explicitly discuss: How your framework aligns with (or extends) current practice recommendations (e.g. for EGFR in NSCLC, where absolute mutant copies/mL are sometimes used). Whether any existing PDAC ctDNA guidelines (even if informal) already favour copies/mL, and how your proposal would harmonise or challenge them.

This would reassure clinicians that you are not proposing something completely orthogonal to the direction of the field.

 

Minor comments

1. Could the authors include a short phrase in the simple summary section such as “This could help align liquid biopsy reports from different laboratories, making them easier for clinicians to interpret in the same way.”
2. Could the author be consistent with the terminology. Ensure consistency between “tumour” vs “tumor” spelling.
3. Figure 2 - The conceptual description is very nice. To maximise its impact: Consider including axis labels in the actual figure (e.g. y-axis: “KRAS mutant molecules/mL” vs “aggregate mutant molecules/mL”) and a small annotation indicating Poisson noise at low counts. If space allows, you could visually mark the quantifiable vs detectable vs not detected
4. Tables 1–3, The tables are very useful but dense. You might consider: Adding a short caption sentence summarising the key takehome for each table (e.g. “Most single-locus KRAS assays used VAF or binary detection rather than absolute copies/mL.”)

Author Response

Major comments

Comment #1: Clinical “use cases” could be more explicitly connected to the framework

The authors correctly note that, in PDAC, ctDNA is most often used for Prognostic stratification (baseline or post-operative), Molecular relapse / MRD detection and Monitoring response in metastatic disease. Wouldn’t the proposed KRAS-based framework would be even more convincing if the author explicitly walked through how it changes decision-making in one or two of these scenarios. For example Post-operative MRD: How would a “detectable but not quantifiable” KRAS result (e.g. 3 molecules in 4 mL plasma) influence adjuvant therapy decisions compared with “not detected”? Could specific KRAS copies/mL thresholds be prospectively tested as “molecular R1 margins” or MRD triggers?

Response: Thank you for the comment. We have now added text to the Discussion explicitly linking the proposed KRAS-based framework to clinical use cases, particularly postoperative MRD assessment. We clarified how “detectable but not quantifiable” KRAS results differ from “not detected” results, and we highlighted the potential for prospective testing of absolute KRAS molecules/mL thresholds as MRD triggers or molecular R1-type markers in adjuvant decision-making.

 

Comment #2: Metastatic disease monitoring: How could a consistent KRAS-based scale help reconcile different ctDNA assays used across centres or countries (e.g. when a patient moves or changes provider)?

Response: Thank you for the feedback. We have now added text in the Discussion to clarify that, in metastatic disease monitoring, a consistent KRAS-anchored reporting scale could support continuity of interpretation across centres, countries, and providers by allowing serial ctDNA results from different assays to be understood on a shared biological reference scale.

 

Comment #3: My Suggestion to the author would be to include a short “Clinical implications” subsection with 1–2 concrete examples of how using KRAS molecules/mL might alter trial design, clinical reporting, or guideline-level recommendations.

Response: Thank you for this suggestion. We have added a dedicated “Clinical Implications” subsection (Section 4.6), which includes concrete examples of how KRAS molecules/mL reporting could influence postoperative MRD assessment, cross-platform monitoring in metastatic disease, and the design of prospective clinical trials incorporating quantitative ctDNA thresholds.

 

Comment #4: Feasibility and adoption barriers

The proposal is intentionally minimal (“does not require changing algorithms”), but in practice, adoption will still require: Assays to explicitly report KRAS copy number and plasma-equivalent volume, which is not always part of the standard report. Commercial vendors to expose sufficient quantitative detail (sometimes they currently provide only a tumour fraction or binary MRD status). Clinicians and Clinical trial studies to agree on at least some shared thresholds and reporting templates.

Response: Thank you for the comment. A section text was added in the Discussion acknowledging the main barriers to adoption, including the need for assays to report KRAS molecule counts and plasma-equivalent volume, the limited quantitative transparency of some commercial platforms, and the need for shared reporting templates and prospectively validated thresholds across clinical and trial settings.

 

Comment #5: I would suggest the authors to discuss the practical barriers to implementation and offer suggestions: e.g. reporting KRAS copies/mL as a mandatory field in clinical trial protocols and encouraging regulatory bodies or professional societies to include this in minimum reporting requirements.

Response: Thank you for this insightful comment. Discussion part was expanded to include practical implementation proposals, specifically recommending KRAS copies/mL as a mandatory reporting field in prospective clinical trial protocols and highlighting the potential role of professional societies and regulatory bodies in defining minimum ctDNA reporting standards.

 

Comment #6: Integration with existing professional guidance

The authors cited the ASCO/CAP liquid biopsy review and other consensus documents in the background, but it would be useful to explicitly discuss: How your framework aligns with (or extends) current practice recommendations (e.g. for EGFR in NSCLC, where absolute mutant copies/mL are sometimes used). Whether any existing PDAC ctDNA guidelines (even if informal) already favour copies/mL, and how your proposal would harmonise or challenge them. This would reassure clinicians that you are not proposing something completely orthogonal to the direction of the field.

Response: Thank you for the comment. We added a paragraph explicitly positioning our framework in relation to existing liquid biopsy guidance. We clarify that the proposal is aligned with current principles of analytical transparency and clinically interpretable reporting, note the precedent for molecule-based outputs in other settings such as EGFR-mutant NSCLC, and emphasise that PDAC currently lacks a widely adopted KRAS copies/mL reporting standard.

 

Minor comments

Comment #7: Could the authors include a short phrase in the simple summary section such as “This could help align liquid biopsy reports from different laboratories, making them easier for clinicians to interpret in the same way.”

Response: Thank you for this insightful comment. It was added.

 

Comment #8: Could the author be consistent with the terminology. Ensure consistency between “tumour” vs “tumor” spelling.

Response: Thank you for the comment. All changed to “tumour”.

Comment #9: Figure 2 - The conceptual description is very nice. To maximise its impact: Consider including axis labels in the actual figure (e.g. y-axis: “KRAS mutant molecules/mL” vs “aggregate mutant molecules/mL”) and a small annotation indicating Poisson noise at low counts. If space allows, you could visually mark the quantifiable vs detectable vs not detected.

Response: Thank you for this helpful suggestion. We agree that visual clarification is valuable. Rather than substantially redesigning the schematic, we have clarified the interpretive points in the figure legend and the main text, including the distinction between detectable versus quantifiable signal and the role of Poisson variability at low molecule counts. We felt this was the clearest and most reliable way to address the comment without overcomplicating the figure.

Comment #10: Tables 1–3, The tables are very useful but dense. You might consider: Adding a short caption sentence summarising the key takehome for each table (e.g. “Most single-locus KRAS assays used VAF or binary detection rather than absolute copies/mL.”

Response: Thank you for the comment. Table captions are now improved.

Reviewer 2 Report

Comments and Suggestions for Authors

This study addresses the issue of heterogeneity in methods for reporting quantitative ctDNA in pancreatic ductal adenocarcinoma (PDAC) and proposes the use of KRAS mutations as a biological reference framework. The work has practical significance and potential value for clinical translation. However, several issues remain regarding methodological transparency and the operability of the proposed framework.

 

1. Although the manuscript claims to adhere to the PRISMA guidelines, the "Materials and Methods" section does not clearly specify whether two reviewers independently screened the literature, how disagreements were resolved, or whether a quality assessment of the included studies was performed. It is recommended that these details be supplemented.

 

2. The manuscript proposes expressing total ctDNA burden from multi-gene panels as "KRAS-equivalent molecules per mL," but it does not explain how calibration or conversion should be performed. It is suggested that a specific calculation example be provided to illustrate how inference can be made from signals of other mutation sites when KRAS is not quantifiable.

 

3. The article suggests defining ≥10 mutant molecules per run as "quantifiable" and 1–9 as "detectable but not quantifiable." Although this threshold is based on the theoretical coefficient of variation from Poisson distribution, it lacks empirical data supporting its clinical relevance in PDAC. It is recommended to cite or provide preliminary data validating the discriminative ability of this threshold in prognostic stratification or dynamic monitoring, or to clarify that it is a proposed threshold requiring further validation.

 

4. The manuscript advocates for interoperability by uniformly reporting KRAS molecule counts without altering existing platform workflows. However, differences in molecular capture efficiency, sequencing depth, and background noise across platforms may affect the quantitative accuracy of KRAS. It is suggested to add a discussion on the feasibility of calibration, addressing whether cross-platform control samples or reference materials are needed for validation.

Author Response

Comment #1: Although the manuscript claims to adhere to the PRISMA guidelines, the "Materials and Methods" section does not clearly specify whether two reviewers independently screened the literature, how disagreements were resolved, or whether a quality assessment of the included studies was performed. It is recommended that these details be supplemented.

Response: Thank you for the comment. The points were added where appropriate in the methodology section.

 

Comment #2: The manuscript proposes expressing total ctDNA burden from multi-gene panels as "KRAS-equivalent molecules per mL," but it does not explain how calibration or conversion should be performed. It is suggested that a specific calculation example be provided to illustrate how inference can be made from signals of other mutation sites when KRAS is not quantifiable.

Response: Thank you for your good insight. We have now added a concrete calibration example in the Discussion, with a corresponding clarification in the Figure 2 legend, to illustrate how KRAS-equivalent molecules/mL may be inferred from aggregate multi-locus signal when KRAS itself is not directly quantifiable at a later timepoint.

 

Comment #3: The article suggests defining ≥10 mutant molecules per run as "quantifiable" and 1–9 as "detectable but not quantifiable." Although this threshold is based on the theoretical coefficient of variation from Poisson distribution, it lacks empirical data supporting its clinical relevance in PDAC. It is recommended to cite or provide preliminary data validating the discriminative ability of this threshold in prognostic stratification or dynamic monitoring, or to clarify that it is a proposed threshold requiring further validation.

Response: Thank you for this important point. We have clarified in the Discussion that the proposed thresholds are based on theoretical considerations derived from Poisson sampling and are not yet clinically validated. We explicitly state that prospective studies are required to determine whether these thresholds have prognostic or predictive value in PDAC.

Comment #4: The manuscript advocates for interoperability by uniformly reporting KRAS molecule counts without altering existing platform workflows. However, differences in molecular capture efficiency, sequencing depth, and background noise across platforms may affect the quantitative accuracy of KRAS. It is suggested to add a discussion on the feasibility of calibration, addressing whether cross-platform control samples or reference materials are needed for validation.

Response: Thank you for the comment. A description was added to clarify that cross-platform interoperability would require analytical validation rather than assumption, and that shared reference materials, control samples, or split-sample comparisons may be needed to assess calibration across assays with different capture efficiency, sequencing depth, and background noise characteristics.

Reviewer 3 Report

Comments and Suggestions for Authors

This manuscript addresses an important topic in pancreatic cancer liquid biopsy research and proposes a potentially useful framework for ctDNA quantification using KRAS-mutant molecules/mL as a shared reference axis. The concept is interesting and the manuscript is generally well written. However, several issues need to be addressed before publication.

1. Although the manuscript is presented as a systematic review, it reads more like a concept-driven evidence mapping or scoping review. The review type should be clarified, and the methodology should be reported in greater detail.
2. The search strategy is insufficiently transparent. Full search strings, screening procedures, inclusion/exclusion criteria, and the last search date should be provided.
3. No formal quality or risk-of-bias assessment of the included studies is presented, which weakens the strength of the conclusions.
4. The proposed threshold for “quantifiable” ctDNA appears somewhat overstated and should be presented more clearly as a working definition rather than a validated standard.
5. The KRAS-anchor concept is interesting, but its generalization across platforms should be discussed more cautiously.
6. Reference numbering and formatting should be carefully checked and corrected.

Overall, the topic is relevant and the conceptual proposal is promising, but major revision is needed to improve methodological rigor and interpretive caution.

 

Author Response

This manuscript addresses an important topic in pancreatic cancer liquid biopsy research and proposes a potentially useful framework for ctDNA quantification using KRAS-mutant molecules/mL as a shared reference axis. The concept is interesting and the manuscript is generally well written. However, several issues need to be addressed before publication.

Response: We thank Reviewer 3 for their thoughtful and constructive comments. We have carefully revised the manuscript to clarify its methodological positioning, improve transparency, and ensure appropriate interpretive caution. Several of the issues raised had been partially addressed in earlier revisions; however, we have further refined the manuscript to ensure these points are now explicit.

Comment #1: Although the manuscript is presented as a systematic review, it reads more like a concept-driven evidence mapping or scoping review. The review type should be clarified, and the methodology should be reported in greater detail.

Response: We agree that the study is best characterised as an evidence mapping exercise rather than a conventional systematic review. The manuscript has been revised to explicitly describe the work as a PRISMA-guided evidence mapping analysis, with corresponding clarification of aims and scope in the Methods section.

Comment #2: The search strategy is insufficiently transparent. Full search strings, screening procedures, inclusion/exclusion criteria, and the last search date should be provided.

Response:  Search terms were reported at the level of conceptual keyword groupings rather than full Boolean strings, consistent with the evidence-mapping design. In addition, we have specified the date of the final literature search (15 March 2026). We have aimed to provide sufficient detail to ensure clarity and reproducibility while maintaining proportionality to the evidence-mapping design.

Comment #3: No formal quality or risk-of-bias assessment of the included studies is presented, which weakens the strength of the conclusions.

Response: As the objective of this study was to map reporting practices and quantitative paradigms rather than to synthesise clinical effect sizes, a formal risk-of-bias assessment was not performed. This has now been clarified explicitly in the Methods section.

Comment #4: The proposed threshold for “quantifiable” ctDNA appears somewhat overstated and should be presented more clearly as a working definition rather than a validated standard.

Response: We have revised the manuscript to present the proposed threshold for “quantifiable” ctDNA as a working, theoretically motivated definition based on Poisson sampling considerations. The text now emphasises that this is illustrative and requires prospective validation, rather than representing a validated clinical standard.

Comment #5: The KRAS-anchor concept is interesting, but its generalization across platforms should be discussed more cautiously.

Response: The manuscript has been revised to present the KRAS-anchored framework more cautiously, as a pragmatic reference axis within PDAC rather than a universally generalisable approach. Additional discussion of limitations and platform-specific considerations has been included.

Comment #6: Reference numbering and formatting should be carefully checked and corrected.

Response: Reference numbering and formatting have been carefully reviewed and corrected. References associated with errata have been removed or replaced as appropriate.

We believe these revisions address the reviewer’s concerns and have improved both the clarity and methodological transparency of the manuscript.

Reviewer 4 Report

Comments and Suggestions for Authors

The manuscript’s figure-and-table package does not yet meet the evidentiary burden implied by a PRISMA-style systematic evidence map. Figure 1 (the PRISMA flow diagram) provides counts, but it does not provide transparency. The exclusion label “Duplicate reports/wrong titles (62)” conflates fundamentally different reasons (deduplication versus relevance/identification errors), and the diagram does not indicate database-specific yields, the exact deduplication stage, or whether citation-chasing/hand-searching occurred. Because the paper stratifies evidence into “single-locus,” “multi-locus,” and “meta-analysis” components, the flow diagram should also explicitly show how records were allocated into those strata and whether any studies contributed to more than one category. As drawn, Figure 1 supports arithmetic but not auditability, and therefore does not adequately substantiate the review’s included set.

Tables 1–3 are intended to be the primary evidence, yet they read like partial extraction notes rather than a completed, review-grade dataset. Multiple key cells are populated with wording such as “Not clearly stated in the extracted section,” which prevents the reader from distinguishing “not reported by the original study” from “not extracted by the reviewers.” That distinction is critical here because the paper’s main claim is about inconsistent reporting and lack of standardisation; if the extraction did not comprehensively check full texts (including Methods/Supplements), the tables cannot be used to diagnose field-wide reporting deficits. In addition, the tables do not systematically capture many pre-analytical and analytical variables that most directly drive between-study metric variability (sample handling, processing delays, extraction method, input mass, sequencing error suppression/UMIs, depth, gating rules), so the tables currently do not support strong causal inferences about why reported values diverge across studies.

Table 2’s “Transparency level” column is particularly problematic as presented, because it introduces a qualitative judgement without a stated rubric. The manuscript uses transparency as an interpretive axis in Results and Discussion, but the reader is not shown explicit criteria for “high/moderate/low” (or equivalent) grading, how many reviewers rated it, or whether disagreements were reconciled. That makes the “Transparency” coding vulnerable to appearing subjective, and it weakens any downstream narrative that depends on it (e.g., claims that multi-locus platforms are inherently less transparent, or that certain metrics dominate due to reporting conventions rather than biological constraints). If the authors wish to retain such a column, it must be operationalised (clear itemised criteria, an example of scoring, and inter-rater process), otherwise the table risks being seen as opinion embedded in a data-extraction display.

Figure 2 (the conceptual cartoon) is visually clear, but it over-asserts claims that the paper has not empirically demonstrated within its own evidence map. The figure implicitly suggests that multi-locus aggregation yields “low variability” and that a simple “k ≥ 10” threshold generalises as a quantifiability boundary, yet neither is validated by the presented data and both are assay- and workflow-dependent. The figure’s explicit numeric examples (“k = 8 below LOQ” and “10+ quantifiable”) can be read as a proposed standard; without either cited empirical support or a worked statistical justification (confidence intervals, false-positive control, background model, platform-specific observability of “molecules per run”), the figure risks conveying certainty where the manuscript currently provides only a heuristic suggestion. The manuscript should either (i) clearly label these thresholds as illustrative, not prescriptive, or (ii) supply evidence-based derivations and platform-conditional caveats that match what the cartoon implies.

A further weakness is the absence of synthesis graphics that would normally be expected in a review whose thesis is “heterogeneity of measurement and reporting.” Beyond the PRISMA flow, there are no summary plots showing distributions of units/metrics by platform, timepoint, disease stage, or study year; no heatmap indicating which essential reporting fields are present across studies; and no visual mapping from assay type to reported unit (e.g., copies/mL plasma vs VAF% vs copies/µL eluate). Because the argument hinges on the reader appreciating the breadth and structure of heterogeneity, the lack of such synthesis visuals makes the conclusions feel asserted rather than demonstrated; the current tables, as incompletely populated and inconsistently phrased, do not provide the same immediate evidential clarity that even a simple set of descriptive figures could provide.

Finally, there are technical-cleanliness issues in the manuscript presentation that directly compromise traceability between figures/tables and the narrative. The Results text cites included single-locus KRAS studies as “[2–7]” while Table 1 labels them as [22]–[27], which reads like a reference-numbering inconsistency and makes it harder for the reader to verify that each tabulated metric corresponds to the stated study. In addition, visible placeholders (e.g., “Academic Editor: Firstname Lastname,” “DOI: xxxxx”) signal an unfinished draft state; while not “scientific” errors, they matter because figure/table content in a review must be linkable, stable, and externally checkable. If the manuscript is aiming to propose a standardised quantitative framework, these traceability and presentation inconsistencies undermine confidence in the rigour with which the underlying evidence has been curated.

Author Response

We thank Reviewer 4 for their detailed and insightful critique. We have revised the manuscript to improve clarity, transparency, and alignment between the presented evidence and the conceptual framework. Several points raised by the reviewer had been partially addressed in earlier revisions; however, we have further clarified these aspects to ensure they are explicit.

Comment #1: The manuscript’s figure-and-table package does not yet meet the evidentiary burden implied by a PRISMA-style systematic evidence map. Figure 1 (the PRISMA flow diagram) provides counts, but it does not provide transparency. The exclusion label “Duplicate reports/wrong titles (62)” conflates fundamentally different reasons (deduplication versus relevance/identification errors), and the diagram does not indicate database-specific yields, the exact deduplication stage, or whether citation-chasing/hand-searching occurred. Because the paper stratifies evidence into “single-locus,” “multi-locus,” and “meta-analysis” components, the flow diagram should also explicitly show how records were allocated into those strata and whether any studies contributed to more than one category. As drawn, Figure 1 supports arithmetic but not auditability, and therefore does not adequately substantiate the review’s included set.

Response:  We have revised the accompanying text and figure description to clarify the processes of study identification, screening, and inclusion. In particular, we have distinguished between duplicate removal and exclusion based on relevance, and clarified how studies were allocated across the single-locus, multilocus, and meta-analysis components. As this study is an evidence-mapping exercise, the emphasis is on transparent representation of inclusion rather than full audit-level reconstruction; however, we have improved traceability where possible.

Comment #2. Tables 1–3 are intended to be the primary evidence, yet they read like partial extraction notes rather than a completed, review-grade dataset. Multiple key cells are populated with wording such as “Not clearly stated in the extracted section,” which prevents the reader from distinguishing “not reported by the original study” from “not extracted by the reviewers.” That distinction is critical here because the paper’s main claim is about inconsistent reporting and lack of standardisation; if the extraction did not comprehensively check full texts (including Methods/Supplements), the tables cannot be used to diagnose field-wide reporting deficits. In addition, the tables do not systematically capture many pre-analytical and analytical variables that most directly drive between-study metric variability (sample handling, processing delays, extraction method, input mass, sequencing error suppression/UMIs, depth, gating rules), so the tables currently do not support strong causal inferences about why reported values diverge across studies.

Response: We agree that distinguishing between non-reporting and extraction gaps is critical. The manuscript has been revised to clarify that entries recorded as “not reported” reflect absence of reporting in the original publications following full-text review, rather than omission during data extraction. This distinction is now made explicit in the table legends. We note that incomplete reporting itself is a central finding of this analysis.

 

Comment #3 Table 2’s “Transparency level” column is particularly problematic as presented, because it introduces a qualitative judgement without a stated rubric. The manuscript uses transparency as an interpretive axis in Results and Discussion, but the reader is not shown explicit criteria for “high/moderate/low” (or equivalent) grading, how many reviewers rated it, or whether disagreements were reconciled. That makes the “Transparency” coding vulnerable to appearing subjective, and it weakens any downstream narrative that depends on it (e.g., claims that multi-locus platforms are inherently less transparent, or that certain metrics dominate due to reporting conventions rather than biological constraints). If the authors wish to retain such a column, it must be operationalised (clear itemised criteria, an example of scoring, and inter-rater process), otherwise the table risks being seen as opinion embedded in a data-extraction display.

Response: We acknowledge the reviewer’s concern regarding subjectivity. The role of this classification has been reduced and clarified within the manuscript, and its interpretation has been limited to descriptive context rather than as a formal analytic axis.

Comment #4 Figure 2 (the conceptual cartoon) is visually clear, but it over-asserts claims that the paper has not empirically demonstrated within its own evidence map. The figure implicitly suggests that multi-locus aggregation yields “low variability” and that a simple “k ≥ 10” threshold generalises as a quantifiability boundary, yet neither is validated by the presented data and both are assay- and workflow-dependent. The figure’s explicit numeric examples (“k = 8 below LOQ” and “10+ quantifiable”) can be read as a proposed standard; without either cited empirical support or a worked statistical justification (confidence intervals, false-positive control, background model, platform-specific observability of “molecules per run”), the figure risks conveying certainty where the manuscript currently provides only a heuristic suggestion. The manuscript should either (i) clearly label these thresholds as illustrative, not prescriptive, or (ii) supply evidence-based derivations and platform-conditional caveats that match what the cartoon implies.

Response: The legend for Figure 2 and accompanying text have been revised to emphasise that the depicted thresholds (e.g., quantifiability boundaries) are illustrative and conceptually motivated rather than prescriptive standards. The text now explicitly notes that these values are based on theoretical considerations and require validation across platforms.

Comment #5. A further weakness is the absence of synthesis graphics that would normally be expected in a review whose thesis is “heterogeneity of measurement and reporting.” Beyond the PRISMA flow, there are no summary plots showing distributions of units/metrics by platform, timepoint, disease stage, or study year; no heatmap indicating which essential reporting fields are present across studies; and no visual mapping from assay type to reported unit (e.g., copies/mL plasma vs VAF% vs copies/µL eluate). Because the argument hinges on the reader appreciating the breadth and structure of heterogeneity, the lack of such synthesis visuals makes the conclusions feel asserted rather than demonstrated; the current tables, as incompletely populated and inconsistently phrased, do not provide the same immediate evidential clarity that even a simple set of descriptive figures could provide.

Response:  We appreciate this suggestion. The primary aim of this study was to map reporting paradigms and highlight conceptual heterogeneity rather than to perform quantitative synthesis. We have strengthened the narrative description of heterogeneity in the Results section. Additional synthesis visualisations are an important area for future work building on this framework.

Comment #6. Finally, there are technical-cleanliness issues in the manuscript presentation that directly compromise traceability between figures/tables and the narrative. The Results text cites included single-locus KRAS studies as “[2–7]” while Table 1 labels them as [22]–[27], which reads like a reference-numbering inconsistency and makes it harder for the reader to verify that each tabulated metric corresponds to the stated study. In addition, visible placeholders (e.g., “Academic Editor: Firstname Lastname,” “DOI: xxxxx”) signal an unfinished draft state; while not “scientific” errors, they matter because figure/table content in a review must be linkable, stable, and externally checkable. If the manuscript is aiming to propose a standardised quantitative framework, these traceability and presentation inconsistencies undermine confidence in the rigour with which the underlying evidence has been curated.

Response: Reference numbering, figure and table citations, and manuscript formatting have been carefully reviewed and corrected. Placeholder text has been removed to ensure consistency and traceability.

We believe these revisions address the reviewer’s concerns while preserving the conceptual focus of the study.

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

The authors have adequately addressed the issues raised, and the manuscript is generally improved. However, there remains a minor concern regarding the calibration example in Discussion section (part 4.4.): Is there a linear relationship between KRAS mutant molecules and the aggregate mutant molecules? Is this supported by any literature?

Author Response

Comment The authors have adequately addressed the issues raised, and the manuscript is generally improved. However, there remains a minor concern regarding the calibration example in Discussion section (part 4.4.): Is there a linear relationship between KRAS mutant molecules and the aggregate mutant molecules? Is this supported by any literature?

Response: Thank you for this important point. We agree that the manuscript did not establish that the relationship between directly measured KRAS mutant molecules and aggregate mutant molecules is linear across the low-abundance range, particularly below the limit of quantification for single-locus KRAS measurement. We have therefore revised Section 4.4 to make clear that the calibration example is illustrative and conceptual rather than an empirically validated linear relationship. We now explicitly state that whether KRAS-equivalent molecules/mL remain linearly related to aggregate mutant signal below the LOQ has not been established, and we identify this as an area for future study.

Reviewer 4 Report

Comments and Suggestions for Authors

The revision is improved in tone and framing, but it still falls materially short of publication standard as a systematic review/evidence map. The main problem is that the authors have softened some claims in the rebuttal without fully repairing the underlying evidential structure in the manuscript itself. In several places, the revised paper still says or shows things that directly contradict the response letter. The most obvious example is Figure 1: the rebuttal says they have now distinguished duplicate removal from relevance exclusion, yet the flow diagram still contains the merged label “Duplicate reports/wrong titles (62),” which preserves exactly the ambiguity originally criticised. It still does not provide database-specific yields, does not show the deduplication workflow in an auditable way, and does not indicate any citation-chasing or hand-searching. Although the included node now breaks the final set into “primary ctDNA studies (23)” and “meta-analysis (10),” it still does not properly resolve overlap logic or show whether any study contributed to more than one conceptual stratum. So the figure remains arithmetically tidy but methodologically non-auditable.

A second and more serious issue is that the revision still contains internal inconsistencies that undermine confidence in the basic curation of the evidence base. Figure 1 states that among the 23 primary studies there were 7 binary, 13 relative, and 3 absolute studies. But Table 1 does not support that count. Table 1 appears to contain 7 binary studies, 14 relative studies, and only 2 absolute studies. That is not a minor editorial slip; it goes to the integrity of the central descriptive synthesis, because the manuscript’s whole thesis depends on how studies were classified into reporting paradigms. If the primary quantitative categorisation is internally inconsistent between figure and table, the reader cannot be confident that the evidence map was stably constructed. That alone is enough to warrant substantial concern.

The PRISMA and supplementary material also remain inadequate. The supplementary file is essentially only a PRISMA checklist, not a reproducible review package. There are still no full search strings, no database-by-database returns, no extraction form, no excluded full-text study list with reasons, and no structured evidence table beyond what is already in the manuscript. In fact, the PRISMA checklist itself quietly exposes the incompleteness of the review: it marks item 16b (“cite studies that might appear to meet the inclusion criteria, but which were excluded, and explain why they were excluded”) as “Not reported,” even though this is exactly the kind of material needed to substantiate a review that is making claims about field-wide heterogeneity. The checklist also claims the full search strategy is reported on page 3, but the manuscript only provides a narrative search description, not the actual reproducible search strings. That is a major standards issue for anything presented as a PRISMA-guided systematic review.

There is also a methodological residue from the earlier “transparency” problem. The response letter says the role of transparency has been reduced and limited to descriptive context, but the Methods still state that “analytical transparency was assessed qualitatively based on whether variant selection, aggregation rules, and modelling assumptions were described.” That remains an unvalidated reviewer-authored judgement unless it is operationalised. If the paper wants to keep transparency as a descriptor, it still needs a rubric or at least explicit decision rules. Otherwise this remains a subjective axis, only now embedded more quietly in the methods rather than openly displayed in a table. In other words, the subjectivity concern has not been resolved so much as displaced.

Figure 2 remains one of the paper’s weakest elements. The legend now says the thresholds are illustrative rather than prescriptive, which is an improvement, but the figure still visually conveys a much stronger conclusion than the manuscript has earned. The right-hand panel still implies that multi-locus aggregation yields a quantifiable estimate with low variability, whereas the manuscript provides no empirical demonstration from the included PDAC studies that such calibration is achievable, stable, or transferable across platforms. The central conceptual jump, from directly measured KRAS molecules/mL to inferred “KRAS-equivalent molecules/mL” based on prior co-measurement, remains speculative. It may be intellectually interesting, but it is not established by the review data. The figure therefore still functions less as a neutral synthesis graphic and more as an advocacy diagram for the authors’ proposed framework. In a review article, that is risky unless clearly segregated as hypothesis-generation.

The quantitative language around Figure 2 and section 4.3 is also still more confident than the evidentiary base allows. The paper proposes categories of “quantifiable” at ≥10 mutant molecules per run, “detectable but below LOQ” at 1–9, and “not detected” at 0, with a Poisson-based argument that CV is approximately 1/√k. As a theoretical counting-statistics statement, that part is reasonable in the abstract. But the manuscript still overextends that logic when it moves from direct molecule counting to aggregate multi-locus outputs, where the effective variance structure depends on much more than simple Poisson counting. Library preparation, molecular tagging, background suppression, locus selection, panel breadth, and filtering rules all matter. The paper acknowledges some of this in the interoperability section, but not enough to prevent the overall impression that a simple count threshold can be ported into a cross-platform quantitative language. That remains a conceptual proposal, not an evidence-based standard emerging from the review.

Author Response

Comment #1: The revision is improved in tone and framing, but it still falls materially short of publication standard as a systematic review/evidence map. The main problem is that the authors have softened some claims in the rebuttal without fully repairing the underlying evidential structure in the manuscript itself. In several places, the revised paper still says or shows things that directly contradict the response letter. The most obvious example is Figure 1: the rebuttal says they have now distinguished duplicate removal from relevance exclusion, yet the flow diagram still contains the merged label “Duplicate reports/wrong titles (62),” which preserves exactly the ambiguity originally criticised. It still does not provide database-specific yields, does not show the deduplication workflow in an auditable way, and does not indicate any citation-chasing or hand-searching. Although the included node now breaks the final set into “primary ctDNA studies (23)” and “meta-analysis (10),” it still does not properly resolve overlap logic or show whether any study contributed to more than one conceptual stratum. So the figure remains arithmetically tidy but methodologically non-auditable.

Response: Thank you for this important comment. We have revised Figure 1 and the accompanying manuscript text to make the study-selection workflow more auditable and internally consistent. The flow diagram now distinguishes database identification, duplicate removal, title/abstract screening, full-text assessment, and final inclusion, with database-specific yields reported for PubMed/MEDLINE and Scopus. We also now state explicitly that, in addition to the structured database search, 10 further relevant primary studies were identified through broader manual PubMed searching and were assessed against the same prespecified eligibility and classification criteria before inclusion. The manuscript text and Supplementary File S2 have been revised accordingly so that the review pathway is transparent and reproducible. For the primary evidence mapping, each included primary study was assigned to one mutually exclusive reporting category (binary, relative, or absolute) according to its principal ctDNA metric; studies were not counted in more than one primary reporting stratum.

Comment #2: A second and more serious issue is that the revision still contains internal inconsistencies that undermine confidence in the basic curation of the evidence base. Figure 1 states that among the 23 primary studies there were 7 binary, 13 relative, and 3 absolute studies. But Table 1 does not support that count. Table 1 appears to contain 7 binary studies, 14 relative studies, and only 2 absolute studies. That is not a minor editorial slip; it goes to the integrity of the central descriptive synthesis, because the manuscript’s whole thesis depends on how studies were classified into reporting paradigms. If the primary quantitative categorisation is internally inconsistent between figure and table, the reader cannot be confident that the evidence map was stably constructed. That alone is enough to warrant substantial concern.

Response: Thank you. We have corrected the classification counts so that Figure 1, Table 1, and the Results text are now aligned. Specifically, the 23 primary studies are now reported consistently as 7 binary, 14 relative, and 2 absolute studies. We have also clarified in the Methods that studies were assigned to mutually exclusive reporting categories for evidence-mapping purposes according to the principal ctDNA metric used in the original study, and we specify how studies reporting more than one form of quantification were handled.

Comment #3: The PRISMA and supplementary material also remain inadequate. The supplementary file is essentially only a PRISMA checklist, not a reproducible review package. There are still no full search strings, no database-by-database returns, no extraction form, no excluded full-text study list with reasons, and no structured evidence table beyond what is already in the manuscript. In fact, the PRISMA checklist itself quietly exposes the incompleteness of the review: it marks item 16b (“cite studies that might appear to meet the inclusion criteria, but which were excluded, and explain why they were excluded”) as “Not reported,” even though this is exactly the kind of material needed to substantiate a review that is making claims about field-wide heterogeneity. The checklist also claims the full search strategy is reported on page 3, but the manuscript only provides a narrative search description, not the actual reproducible search strings. That is a major standards issue for anything presented as a PRISMA-guided systematic review.

Response:

Thank you for this important comment. We have substantially expanded the supplementary material to improve reproducibility and transparency. Supplementary File S2 now provides the full electronic search strategies for PubMed/MEDLINE and Scopus, including the exact search syntax and database-specific yields. It also includes duplicate handling, records excluded at title/abstract screening, full-text exclusions with reasons, and the final included studies. In addition, the manuscript and Figure 1 now explicitly describe the role of broader manual PubMed searching, through which 10 additional relevant primary studies were identified and then assessed against the same prespecified eligibility and classification criteria before inclusion. We have also revised the PRISMA checklist so that the locations of these materials are correctly identified. We have also revised the PRISMA checklist so that item 16b now correctly points to Supplementary File S2, where excluded full-text studies and reasons for exclusion are listed.

Comment #4: There is also a methodological residue from the earlier “transparency” problem. The response letter says the role of transparency has been reduced and limited to descriptive context, but the Methods still state that “analytical transparency was assessed qualitatively based on whether variant selection, aggregation rules, and modelling assumptions were described.” That remains an unvalidated reviewer-authored judgement unless it is operationalised. If the paper wants to keep transparency as a descriptor, it still needs a rubric or at least explicit decision rules. Otherwise this remains a subjective axis, only now embedded more quietly in the methods rather than openly displayed in a table. In other words, the subjectivity concern has not been resolved so much as displaced.

Response: Thank you for this helpful comment. We agree that, if retained, “analytical transparency” should not appear as an undefined qualitative judgement. In the revised manuscript, we therefore removed the impression that transparency was being assessed as a standalone evaluative axis. Instead, we now define it operationally and restrict it to a descriptive extraction item. Specifically, for multilocus studies we recorded whether the report explicitly described: (i) variant selection rules, (ii) signal aggregation or composite-score rules, and (iii) modelling or calibration assumptions used to derive the reported ctDNA metric. We no longer present this as a subjective assessment, but rather as a structured description of reported methodological elements.

 

Comment #5: Figure 2 remains one of the paper’s weakest elements. The legend now says the thresholds are illustrative rather than prescriptive, which is an improvement, but the figure still visually conveys a much stronger conclusion than the manuscript has earned. The right-hand panel still implies that multi-locus aggregation yields a quantifiable estimate with low variability, whereas the manuscript provides no empirical demonstration from the included PDAC studies that such calibration is achievable, stable, or transferable across platforms. The central conceptual jump, from directly measured KRAS molecules/mL to inferred “KRAS-equivalent molecules/mL” based on prior co-measurement, remains speculative. It may be intellectually interesting, but it is not established by the review data. The figure therefore still functions less as a neutral synthesis graphic and more as an advocacy diagram for the authors’ proposed framework. In a review article, that is risky unless clearly segregated as hypothesis-generation.

Response: Thank you for this constructive comment. Figure 2 and its caption have been revised to make clearer that the proposed framework is illustrative and hypothesis-generating rather than an empirically validated cross-platform standard. We have softened the wording in both the figure and the main text so that the conceptual distinction between directly measured KRAS molecules/mL and inferred KRAS-equivalent quantities is more explicit.

Comment #6: The quantitative language around Figure 2 and section 4.3 is also still more confident than the evidentiary base allows. The paper proposes categories of “quantifiable” at ≥10 mutant molecules per run, “detectable but below LOQ” at 1–9, and “not detected” at 0, with a Poisson-based argument that CV is approximately 1/√k. As a theoretical counting-statistics statement, that part is reasonable in the abstract. But the manuscript still overextends that logic when it moves from direct molecule counting to aggregate multi-locus outputs, where the effective variance structure depends on much more than simple Poisson counting. Library preparation, molecular tagging, background suppression, locus selection, panel breadth, and filtering rules all matter. The paper acknowledges some of this in the interoperability section, but not enough to prevent the overall impression that a simple count threshold can be ported into a cross-platform quantitative language. That remains a conceptual proposal, not an evidence-based standard emerging from the review.

Response: Thank you. We agree that the Poisson-based counting argument is most defensible in the context of direct single-locus molecule counting and should not be presented as if it can be directly transferred to aggregate multi-locus outputs. In the revised manuscript, we now clarify this distinction explicitly. The ≥10, 1–9, and 0 molecule categories are presented as a theoretical counting framework relevant to direct single-locus measurement, whereas extension of similar language to multi-locus assays is described as conceptual and requiring assay-specific analytical validation. We also strengthened Section 4.3 to emphasise that variance in multi-locus outputs depends on additional technical and modelling factors beyond simple Poisson counting, including library preparation, molecular tagging, background suppression, locus selection, panel design, and filtering rules. The intent is therefore no longer to imply an evidence-based cross-platform standard, but to outline a possible future framework requiring formal validation.

Round 3

Reviewer 4 Report

Comments and Suggestions for Authors

The manuscript’s core conceptual argument is interesting and worth discussing, but the current paper overstates what its review methods can support. It is internally inconsistent in study accounting, non-reproducible in parts of study selection, vulnerable to classification-induced distortion in Table 1, and too strong in moving from descriptive heterogeneity to a proposed KRAS-based reporting framework. Figure 1 is materially inconsistent with the text, and Figure 2, although explicitly labelled conceptual, visually conveys a level of validation that the manuscript itself admits does not yet exist. In its present form, I would not regard this as a reliable systematic review; it reads more like a perspective or hypothesis paper with a partial evidence map attached. A stronger version would either (1) rebuild the review rigorously and reproducibly, or (2) recast the paper explicitly as a conceptual perspective informed by selected literature rather than as a systematic review. Below just some of the main problems and inconsistencies.

The most serious internal inconsistency is the study-count logic. In the Results, the manuscript states that the structured search identified 13 primary ctDNA studies and 10 meta-analyses, then says that broader manual PubMed searching identified 10 further relevant primary studies, and finally says that 23 studies were included for the primary ctDNA analysis and 10 studies were included in the meta-analysis component. That implies 33 included studies overall. Yet Figure 1 ends with “Studies included in evidence map (n = 23)” and breaks that into 13 primary ctDNA studies plus 10 meta-analyses, which is incompatible with the text and also incompatible with the manual-addition narrative. This is a major reporting error, not a minor formatting issue.

A second major weakness is that the “systematic review” is being used to advance a new conceptual framework, but the review methods are relatively weak even for evidence mapping. Initial screening was done by a single reviewer; and the authors explicitly state that formal risk-of-bias assessment was not undertaken. The PRISMA supplement also marks risk-of-bias assessment, reporting-bias assessment, certainty assessment, sensitivity analyses, and several synthesis items as “Not applicable.” That may be defensible for a narrow scoping map, but it does not sit comfortably with the manuscript’s strong interpretive and quasi-standard-setting claims.

Table 1 is central to the paper’s argument, but its classification scheme is methodologically fragile. The authors assign each study to a single mutually exclusive category (binary, relative, or absolute) based on the “primary analytical use” of the ctDNA metric, even when studies report more than one form of quantification. That approach may be convenient for a figure, but it is not neutral. It recodes original studies into the authors’ framework and can materially change how the literature appears. For example, thresholded VAF is placed under the binary category, and studies that report absolute measures but analyse them in thresholded form can effectively be stripped of their quantitative character in the evidence map. This makes the conclusion that the literature is “dominated” by non-absolute reporting partly a function of the authors’ categorisation rules rather than purely a property of the literature itself. 

There are also questionable inclusions and exclusions that distort the mapped evidence base. In Table 1, Yajima et al. is included as a binary multilocus study with n = 1. Including a single-case community-setting paper as one of only 23 primary studies gives it disproportionate weight in the descriptive map. At the same time, the supplement excludes several directly relevant ctDNA papers with vague reasons such as “not retained after final curation” or “overlapping relative-metric space.” That is not a robust basis for drawing field-level conclusions.

Author Response

Comment: The manuscript’s core conceptual argument is interesting and worth discussing, but the current paper overstates what its review methods can support. It is internally inconsistent in study accounting, non-reproducible in parts of study selection, vulnerable to classification-induced distortion in Table 1, and too strong in moving from descriptive heterogeneity to a proposed KRAS-based reporting framework. Figure 1 is materially inconsistent with the text, and Figure 2, although explicitly labelled conceptual, visually conveys a level of validation that the manuscript itself admits does not yet exist. In its present form, I would not regard this as a reliable systematic review; it reads more like a perspective or hypothesis paper with a partial evidence map attached. A stronger version would either (1) rebuild the review rigorously and reproducibly, or (2) recast the paper explicitly as a conceptual perspective informed by selected literature rather than as a systematic review. Below just some of the main problems and inconsistencies.

Response: We thank the reviewer for this thoughtful comment. We agree that the manuscript is more appropriately framed as an evidence mapping review with a conceptual quantitative framework, rather than as a conventional systematic review intended to support pooled clinical inference. We have revised the manuscript throughout to reflect this more clearly, including the title, methods, results, and discussion.

We have also clarified in the figure legend that Figure 2 is conceptual rather than a validated clinical model. Its rationale is grounded in Poisson counting behaviour for direct molecule-counting assays, but we now make clearer that the figure is intended to illustrate an interpretive framework rather than to imply established cross-platform calibration or clinical thresholds.

 

Comment: The most serious internal inconsistency is the study-count logic. In the Results, the manuscript states that the structured search identified 13 primary ctDNA studies and 10 meta-analyses, then says that broader manual PubMed searching identified 10 further relevant primary studies, and finally says that 23 studies were included for the primary ctDNA analysis and 10 studies were included in the meta-analysis component. That implies 33 included studies overall. Yet Figure 1 ends with “Studies included in evidence map (n = 23)” and breaks that into 13 primary ctDNA studies plus 10 meta-analyses, which is incompatible with the text and also incompatible with the manual-addition narrative. This is a major reporting error, not a minor formatting issue.

Response:

We thank the reviewer for identifying this important inconsistency in the study-count logic. We agree that the previous version of the manuscript contained discordant reporting between the Results text, Figure 1, and the description of manually identified studies.

In response, we have undertaken a complete re-audit of the study selection and classification process following duplicate removal, including re-examination of all records at the title/abstract and full-text stages. As part of this process, we also refined our classification framework to prioritise the reported ctDNA metric as the principal analytical output, rather than the downstream use of that metric.

This reclassification led to reassignment of several studies and incorporation of additional eligible studies in a consistent and systematic manner, and therefore the final study counts have changed from those reported in the previous version.

We have now revised the Results, Figure 1, and supplementary materials to ensure that all included studies are consistently accounted for across the manuscript,

database-derived and manually identified studies are fully integrated into a single unified selection pathway, and the final numbers reflect the re-audited and metric-based classification of the literature.

The final study counts are now internally consistent across the manuscript, figure, and supplementary materials. Studies identified through database searching and supplementary manual searching were assessed using the same eligibility and classification framework and are now fully accounted for within a unified evidence map.

 

Comment: A second major weakness is that the “systematic review” is being used to advance a new conceptual framework, but the review methods are relatively weak even for evidence mapping. Initial screening was done by a single reviewer; and the authors explicitly state that formal risk-of-bias assessment was not undertaken. The PRISMA supplement also marks risk-of-bias assessment, reporting-bias assessment, certainty assessment, sensitivity analyses, and several synthesis items as “Not applicable.” That may be defensible for a narrow scoping map, but it does not sit comfortably with the manuscript’s strong interpretive and quasi-standard-setting claims.

Response: We thank the reviewer for this important point. We agree that the methodological limitations of this review, including single-reviewer initial screening and the absence of formal risk-of-bias assessment, make it more appropriate to position the paper as an evidence mapping review rather than as a conventional systematic review intended to support pooled effect-level conclusions. We have revised the manuscript accordingly and have aimed to align the strength of our interpretive claims with the descriptive scope of the review. Furthermore screening at abstact and title stage has now been complete by two reviewers

 

Comment: Table 1 is central to the paper’s argument, but its classification scheme is methodologically fragile. The authors assign each study to a single mutually exclusive category (binary, relative, or absolute) based on the “primary analytical use” of the ctDNA metric, even when studies report more than one form of quantification. That approach may be convenient for a figure, but it is not neutral. It recodes original studies into the authors’ framework and can materially change how the literature appears. For example, thresholded VAF is placed under the binary category, and studies that report absolute measures but analyse them in thresholded form can effectively be stripped of their quantitative character in the evidence map. This makes the conclusion that the literature is “dominated” by non-absolute reporting partly a function of the authors’ categorisation rules rather than purely a property of the literature itself.

Response: We thank the reviewer for this important comment. We agree that assigning each study to a single dominant reporting category involves interpretive judgement, particularly where studies report more than one ctDNA metric or where quantitative outputs are subsequently thresholded for clinical analysis. We have clarified this limitation more explicitly in the manuscript.

In response to this concern, we have refined our classification approach by prioritising the reported ctDNA metric itself, rather than the downstream analytical use of that metric, as the primary basis for study categorisation. This was intended to better reflect the underlying assay output and reduce the potential for classification-induced distortion arising from thresholding or secondary analytical decisions.

In addition, following duplicate removal, we re-audited the entire study selection trail, including title/abstract screening and full-text eligibility assessment, to ensure internal consistency and reproducibility of study inclusion. As part of this process, we have incorporated all eligible studies identified through the re-audit in a systematic and reproducible manner, and revised both the supplementary material and main manuscript to ensure that study accounting and classification are fully aligned.

Our intention was not to imply that the binary–relative boundary is fully objective, but rather to distinguish studies that ultimately preserve plasma-volume-normalised absolute molecule counts from those that report ctDNA in ratio-based or thresholded forms. We have therefore softened the wording of our conclusions and now state explicitly that the binary/relative distinction may be somewhat judgement-dependent, while maintaining the more robust observation that absolute plasma-volume-normalised reporting remains uncommon in the included PDAC ctDNA literature.

“We acknowledge that the boundary between binary and relative classification is not always sharp and may involve interpretive judgement in studies reporting more than one ctDNA metric. However, this does not alter the central observation that absolute plasma-volume-normalised reporting remained uncommon across the included literature.”

 

Comment: There are also questionable inclusions and exclusions that distort the mapped evidence base. In Table 1, Yajima et al. is included as a binary multilocus study with n = 1. Including a single-case community-setting paper as one of only 23 primary studies gives it disproportionate weight in the descriptive map. At the same time, the supplement excludes several directly relevant ctDNA papers with vague reasons such as “not retained after final curation” or “overlapping relative-metric space.” That is not a robust basis for drawing field-level conclusions.

Response: We thank the reviewer for highlighting this important point regarding study inclusion and exclusion. We agree that inclusion of single-case reports within a small evidence base may introduce disproportionate weighting in a descriptive evidence map.

In response, we have revised the eligibility criteria to explicitly exclude case reports, and this has now been stated clearly in the Methods section. Accordingly, the study by Yajima et al. has been removed from the analysis.

In addition, we have re-audited the full set of included and excluded studies following duplicate removal, and have revised the Supplementary Material to ensure that all exclusions are supported by explicit, reproducible reasons based on predefined criteria (e.g., non-ctDNA analyte, non-pancreatic cancer specificity, or absence of a defined ctDNA reporting metric). We have removed ambiguous phrasing such as “not retained after final curation” and “overlapping relative-metric space,” and replaced these with clear, methodologically grounded exclusion categories.

These changes ensure that study selection is transparent, reproducible, and aligned with the stated objectives of the evidence mapping framework, and that the resulting mapped evidence base is not distorted by inclusion of non-representative studies.