All reviews of published articles are made public. This includes manuscript files, peer review comments, author rebuttals and revised materials. Note: This was optional for articles submitted before 13 February 2023.
Peer reviewers are encouraged (but not required) to provide their names to the authors when submitting their peer review. If they agree to provide their name, then their personal profile page will reflect a public acknowledgment that they performed a review (even if the article is rejected). If the article is accepted, then reviewers who provided their name will be associated with the article itself.
Both reviewers have carefully evaluated your revised manuscript and are satisfied that you have appropriately addressed their comments. In light of their positive recommendations and the improved clarity and rigor of the work, I am pleased to inform you that your manuscript has been accepted for publication in our journal.
No comment.
No comment.
No comment.
The authors retrospective analyzes the therapeutic performance and adverse event profile of tislelizumab plus lenvatinib in patients with unresectable hepatocellular carcinoma (uHCC), primarily of HBV etiology. Overall, the data is encouraging and the study is well-reported. The revised manuscript can be accepted.
The revised manuscript meets the publication standards.
no comment
'no comment
After careful consideration of the reviewers’ reports, we are inviting a major revision. While the study is of interest, substantial concerns remain regarding, as detailed in the reviewers’ comments. Please address all points comprehensively, provide point-by-point responses for clarity.
**PeerJ Staff Note:** Please ensure that all review and editorial comments are addressed in a response letter and that any edits or clarifications mentioned in the letter are also inserted into the revised manuscript where appropriate.
**Language Note:** The review process has identified that the English language must be improved. PeerJ can provide language editing services - please contact us at [email protected] for pricing (be sure to provide your manuscript number and title). Alternatively, you should make your own arrangements to improve the language quality and provide details in your response letter. – PeerJ Staff
Please see Additional comments.
Please see Additional comments.
Please see Additional comments.
In this study, the authors retrospective analyzes the therapeutic performance and adverse event profile of tislelizumab plus lenvatinib in patients with unresectable hepatocellular carcinoma (uHCC), primarily of HBV etiology. The finding of this study provides real-world evidence regarding this therapeutic strategic for uHCC patients. Among the 163 patients, the ORR was 25.8%, DCR was 67.5%, and median PFS reached 23.1 months. Besides, 16.6% of patients underwent successful conversion therapy and surgical resection. The rate of grade 3–4 TRAEs was limited to 5%. Overall, the data is encouraging and the study is well-reported. However, there are some concerns to be addressed to improve the manuscript.
1.Li et al. reported the efficacy and safety of tislelizumab combined with lenvatinib as first-line treatment for patients with uHCC (doi: (10.1186/s12916-024-03356-5), among which 90.6% of the patients had HBV-related etiology. The authors should focus on discussing the innovations compared with their reports and the special findings of this study.
2.The abbreviations in the Abstract should be provided with full English names. Figures and Tables in the article might be viewed independently. Therefore, all abbreviations used in Figures and Tables should be defined in their legends (or notes). Besides, abbreviation should be defined in the text at first use. Authors should check the whole manuscript.
3.In the methodology section, please provide more details on the patient selection process. According to the patient selection flowchart in Figure 1, 20 patients were excluded due to "without sufficient data." Please briefly specify what key data were missing.
4.In multivariate analysis, liver local therapy was independently associated with improved OS. What are the specific types of local liver therapy? Relevant information should be supplemented in the manuscript?
5.The results show that 89.0% of patients received local liver-directed therapies, which was associated with longer OS in the multivariate analysis. However, the text does not explain what "local liver-directed therapies" entails, nor do the authors discuss this result in greater depth in the "Discussion" section. It is recommended that the authors specify the types of "local liver-directed therapies" (e.g., TACE, ablation, etc.) in the article and explore the potential synergistic effect between local and systemic therapies more thoroughly in the "Discussion."
6.The results show that 16.6% of patients successfully underwent surgical resection. To increase the clinical value of this finding, it is suggested that the authors briefly summarize the key baseline data of these 27 patients in the main text. This may help clinicians identify which subset of patients is more likely to benefit from this regimen.
7.During the discussion, it was suddenly mentioned that in the patient cohort, "no drug withdrawal occurred", which indicates good safety. It is recommended to provide additional details on whether it is necessary to interrupt the dosage of lenvatinib or adjust it to manage TRAEs, as well as the situation when used in combination with TACE. This information is more valuable for guiding clinical practice.
8.The conclusion section states that "Tumor burden, particularly size ≥5 cm and multifocality, was associated with earlier progression." However, according to the results of the article, we see that "multiple lesions" was an independent factor for shorter PFS only in the univariate analysis, but no statistical difference was observed in the multivariate analysis. Please provide a reasonable explanation for this result.
9.The content of the Discussion section is insufficient. That should be revised to describe in more depth concerning the novelty of this study comparing with previous studies, its clinical appliance, as well as directions for future work.
10.Table 3 is not mentioned in the manuscript.
11.The overall language of the article is good. But there are still a few details that need attention. Such as “…employed n the initial systemic treatment…” in line 47-48, “Kaplan3Meier” in line 297. “Tumor size g 5cm group” in line 322. The author should recheck the whole manuscript carefully.
This retrospective study evaluated the combination therapy of tislelizumab and lenvatinib in 163 patients with unresectable hepatocellular carcinoma (uHCC), predominantly HBV-related. The treatment showed meaningful clinical benefits, with an objective response rate (ORR) of 25.8%, disease control rate (DCR) of 67.5%, and a median progression-free survival (PFS) of 23.1 months. Notably, 16.6% of patients underwent successful conversion therapy followed by surgical resection. While larger tumor burden was associated with shorter PFS, it did not significantly affect overall survival (OS). The regimen demonstrated a favorable safety profile, with grade≥3 adverse events occurring in only 5% of patients, supporting its use as first-line therapy in HBV-endemic regions. However, there are still several issues that need to be addressed in this study.
1)The abstract reports a median progression-free survival (PFS) of 23.1 months and notes that median overall survival (OS) was “not estimable” but provides no information on the median follow-up duration of the 163-patient cohort. Follow-up time is critical for interpreting survival endpoints, without it, readers cannot assess whether the “not estimable” OS reflects a truly favorable long-term survival trend or insufficient follow-up to capture mature OS data. This omission weakens the ability to contextualize the regimen’s long-term efficacy and limits comparability with other studies where follow-up duration is explicitly stated.
2)While the introduction thoroughly reviews the current landscape of systemic therapy for uHCC, it does not explicitly state the specific knowledge gap that this study aims to address. The authors mention that real-world data are limited but should more clearly articulate how their study focusing specifically on a predominantly HBV-positive, real-world population treated with tislelizumab (not pembrolizumab or camrelizumab) adds unique and necessary evidence to the field. In addition, the introduction successfully builds a case for the general strategy of combining ICIs with TKIs. However, it provides a comparatively weaker rationale for choosing the specific combination of tislelizumab and lenvatinib. The authors should briefly highlight the pre-clinical or clinical rationale (e.g., unique properties of tislelizumab, synergistic mechanisms specific to this pair) that justifies investigating this particular combination over other ICI-TKI options, especially since it is the focus of the paper.
3)The “Study Population” subsection defines the cohort as patients initiating therapy between January 2021 and June 2025. However, given standard research workflows and the implicit timeline of manuscript preparation (aligned with real-world data collection practicality), data for the period July 2024–June 2025 would not have been accessible or verifiable at the time of study conduct. The manuscript provides no clarification (e.g., whether “June 2025” is a typo for “June 2024”) or explanation of how “future” data was obtained. This inconsistency directly undermines the validity of the dataset, as the core premise of retrospective analysis, relying on already collected, de-identified data is violated, leaving readers unable to trust the completeness or authenticity of the 163-patient cohort.
4)A key secondary outcome of the study is that 16.6% of patients underwent “successful conversion therapy and surgical resection.” However, the “Material and Methods” section fails to outline the explicit criteria used to determine eligibility for conversion therapy (e.g., tumor response thresholds per mRECIST, liver function stability, absence of new PVTT/extrahepatic metastases) or the surgical criteria (e.g., R0 resection requirements, residual liver volume thresholds). This omission is significant: without defining how “success” was operationalized for conversion, readers cannot evaluate whether the 16.6% rate is clinically meaningful (e.g., if resections were curative) or comparable to other studies with different conversion thresholds.
5)The patient selection flow diagram (Fig. 1) notes 20 patients were excluded for “insufficient data,” but the manuscript provides no details on the extent of missing data in the final 163-patient cohort (e.g., missing AFP values, incomplete imaging follow-up for response assessment, lost-to-follow-up for OS/PFS). There is also no description of statistical methods used to address missing data (e.g., listwise deletion, multiple imputation), which is critical for assessing bias in endpoint analyses. Additionally, the study includes 163 patients but offers no sample size justification no power calculation or reference to prior studies to confirm the cohort size is sufficient to detect meaningful differences in key outcomes (e.g., PFS between patients with tumor size <5 cm vs. ≥5 cm) or rare events.
6)While 84.7% of the cohort has HBV-related uHCC (the primary focus of the study), the “Results” section provides no stratified efficacy data for this subgroup, such as ORR, DCR, median PFS, or conversion-to-resection rate compared to non-HBV etiologies (e.g., HCV, “other” causes). Furthermore, the lack of data on HBV-specific factors (e.g., viral load control, antiviral therapy use) precludes an analysis of their association with outcomes. This information is critical for real-world clinical decision-making in HBV-endemic regions, where viral suppression can impact treatment tolerability and efficacy. We recommend that the authors explicitly address this limitation in the Discussion section and comment on its potential impact on the generalizability of the findings.
7)The study highlights that 16.6% of patients underwent surgical resection after conversion therapy, a key finding for curative intent. However, the “Results” section provides no details on critical post-conversion outcomes that define the clinical value of this achievement: (1) pathological response (e.g., major pathological response, complete pathological response) in resected tumors, which correlates with long-term recurrence risk; (2) surgical morbidity/mortality (e.g., 30-day complication rates, in-hospital mortality); (3) margin status (R0 vs. R1 resection), a strong prognostic factor for HCC; and (4) post-resection recurrence-free survival (RFS). Without these data, the “success” of conversion therapy remains superficial, readers cannot determine if resection translated to meaningful long-term benefit or if the regimen’s conversion potential is clinically actionable.
8)The “Results” states median OS was “not estimable within the follow-up period” (Fig. 2A) but fails to provide two critical pieces of information: (1) the median follow-up time for the entire cohort (e.g., “median follow-up of 18 months”) and (2) the proportion of patients censored at the last follow-up (e.g., “70% of patients alive at data cutoff”). Without median follow-up, it is impossible to assess whether the non-estimable OS reflects a truly favorable survival trend (e.g., most patients still alive) or insufficient follow-up (e.g., short-term data with high censoring). Additionally, there is no stratified OS data for high-risk subgroups (e.g., Child-Pugh B, PVTT-positive, extrahepatic metastases), which are critical for identifying patients most likely to benefit from the regimen. This ambiguity limits the utility of the survival data for comparing with other first-line therapies in uHCC.
9)The subgroup analyses presented in the forest plots (Fig. 3-6) show point estimates for different patient categories. However, to confirm that the effect of treatment (or a prognostic factor) truly differs between subgroups, formal tests for interaction should be performed and reported. Without p-values for interaction, the conclusions drawn from subgroup comparisons (e.g., the benefit of liver local therapy) remain suggestive rather than statistically confirmed.
10)The discussion highlights the median PFS of 23.1 months as a favorable outcome compared to other trials (e.g., IMbrave150's 6.8 months). However, the comparison may be misleading without acknowledging key contextual differences: The IMbrave150 regimen (atezolizumab+bevacizumab) is a standard-of-care comparator, and the dramatic difference in PFS (23.1 vs. 6.8 months) raises questions about patient selection, follow-up duration, or assessment intervals. This significant discrepancy should be explicitly addressed rather than presented solely as a strength. The median OS was not reached, which is positive but immature. The discussion should more cautiously interpret survival outcomes and avoid overstating clinical benefits without longer follow-up or maturity in OS data.
11)The discussion does not explore potential biological reasons behind the findings, particularly why tumor burden (size and number) predicts PFS but not OS. This is a critical observation that warrants mechanistic speculation: Could this reflect delayed progression rather than improved survival? Or might subsequent therapies after progression have mitigated the impact of initial tumor burden on OS? Incorporating recent literature on how VEGF inhibition plus immunotherapy might alter tumor immune microenvironments, especially in HBV-related HCC would deepen the discussion and align the results with translational science.
12) The limitations mentioned are overly brief and generic. The following points should be expanded upon: The single-center, retrospective design introduces potential biases in patient selection, treatment administration, and outcome assessment. These should be explicitly listed. The HBV-dominated cohort (84.7%) limits generalizability to non-HBV or Western populations. This should be discussed as a notable limitation, not just a demographic note. Given that tolerability and quality of life are crucial for a first-line regimen, the absence of quality-of-life data or patient-reported outcomes is a limitation; therefore, the authors should clearly acknowledge this in the manuscript.
13) Overall, the writing is clear and professionally presented, making the scientific content accessible. However, minor grammatical inconsistencies and occasional awkward phrasing suggest that thorough proofreading by a native English speaker would further enhance readability and polish.
/
/
/
All text and materials provided via this peer-review history page are made available under a Creative Commons Attribution License, which permits unrestricted use, distribution, and reproduction in any medium, provided the original author and source are credited.