The Effect of Contemporary Brachytherapy Practices on Prognosis in Women with Locally Advanced Cervical Cancer

Round 1

Reviewer 1 Report

This study was described that the utility of BT in patients with locally advanced cervical cancer. This report is interesting for readers. However, the reviewer would like to suggest some critiques as follows.

 

1.      What is “MRI+needles”? The authors should provide a clear definition of this in the text.

2.      On line 27 and 29, the authors should spell out about IQR and CI.

3.      On line 70, “Randomised evidence … is lacking” is unclear.

Author Response

Point 1: What is “MRI+needles”? The authors should provide a clear definition of this in the text. 

Response 1: Thank you for bringing this to our attention. We have tried to clarify this further, as it is one of the most important definitions in our article. The MRI+needles group represents patients with access to (but not necessarily all receiving) state-of-the-art MRI-guided adaptive brachytherapy with combined intracavitary/interstitial technique. Whereas the patients in the MRI group were treated before the use of interstitial needles was introduced at our centre. We have changed our manuscript accordingly, see lines 361-366.

Point 2: On line 27 and 29, the authors should spell out about IQR and CI.

Response 2: We agree with the reviewer that both abbreviations should indeed be clarified on first mention. See the changes made on lines 27-29.

Point 3: On line 70, “Randomised evidence … is lacking” is unclear. 

Response 3:  We have made an effort to write this sentence more clearly and have replaced the sentence (line 80) with the following: “The potential benefit of IGABT over 2D brachytherapy in patients with locally advanced cervical cancer has been evaluated in a few non-randomised studies.” The purpose of this sentence is to emphasise that there are no randomised trials on this topic.

Reviewer 2 Report

 

I want to start by congratulating the authors on this outstanding dataset. Overall, the authors did an excellent job outlining the context and the objective. I do, however, have some severe criticisms, particularly in regard to the analysis that was done:

1.      Given the evidence presented in the introduction and the manner in which the procedures were implemented at the centre, it is expected that MRI+needles will perform better. This prompts me to ponder a crucial query: What is the added value of this work to current knowledge?

2.      The survival curves are nice, but these give an impression of the univariate results, which will be biased. Reason why the multivariable model is quite import to answer your research question. In this regard, I would expect that the exposure of interest (CT, MR, and MRI+needles) would be in the multivariable model for all the outcomes, given the aim of the research. Further, because the baseline characteristics of the three groups vary substantially, the authors must carefully choose the variables to include in the multivariable model. A decision based on literature might be more relevant than a backward selection. In addition, I miss the year of diagnosis as a covariate. This might be a proxy for all changes over time that impact the estimates.

3.      Some results are difficult to understand since the methods section is not fully described. For illustration: It is tough to interpret the results from the Venn diagrams as your main outcomes were time-to-event variables, and it is not explicit in the methods why you present the results in this way. It is also unclear why toxicity was only provided as a frequency per treatment group when the other outcomes (tumor control, disease-free survival, and overall survival) were evaluated and modeled as time-to-event outcomes.

4.  As a minor suggestions, the authors should maintain consistency because it seems they are using 'local control', 'tumor control' and 'failure' to refer to the same concept. For instance, in Table 2, the first outcome is called 'local control'; in the methods, the outcome is defined as 'tumor control', but the title refers to 'failure'. So I guess the authors are referring to the time from diagnosis (local, pelvic, any) to recurrence. Additionally, many of the confounders were not described in the methods (WHO performance score, smoking, hypertension, etc.), and in my opinion, describing how the variables were measured provided insight into the quality of the study.

My suggestion would be to contact an epidemiologist and to ask for some support to analyze this interesting database.

I hope the authors find this revision pertinent and helpful.

 

Author Response

Thank you for your thoughtful and insightful comments. They show that you have read the manuscript carefully and we acknowledge that there are several points that need to be improved. Here are our comments on the points you have raised.

Point 1: Given the evidence presented in the introduction and the manner in which the procedures were implemented at the centre, it is expected that MRI+needles will perform better. This prompts me to ponder a crucial query: What is the added value of this work to current knowledge?

Response 1: To our knowledge, our study is the first to include all three brachytherapy techniques (CT-guided, MRI-guided and MRI-guided with the possibility of interstitial needle insertion) in a multivariable model in order to correct for several potential confounders. Combined intracavitary/interstitial brachytherapy has already been evaluated previously by the (retro)EMBRACE group. They have published several reports on the prognosis of women treated with image-guided brachytherapy. However, a multivariable analysis is lacking for this large multicentre cohort (with a wide range of care practice and differences in case mix). Rijkmans et al performed a single-centre comparison with multivariable analysis similar to our cohort, but as they included 124 patients of whom only 11 were treated with interstitial needles, the effect of this advance in brachytherapy practice could not be evaluated separately. We have tried to develop this further in the manuscript, see lines 1493-1497.

In addition, it is valuable to confirm the results of the retroEMBRACE. The improved oncological outcomes found in this multicentre study seem to be applicable to the patients treated in our centre.

Point 2: The survival curves are nice, but these give an impression of the univariate results, which will be biased. Reason why the multivariable model is quite import to answer your research question. In this regard, I would expect that the exposure of interest (CT, MR, and MRI+needles) would be in the multivariable model for all the outcomes, given the aim of the research. Further, because the baseline characteristics of the three groups vary substantially, the authors must carefully choose the variables to include in the multivariable model. A decision based on literature might be more relevant than a backward selection. In addition, I miss the year of diagnosis as a covariate. This might be a proxy for all changes over time that impact the estimates.

Response 2:

We agree with several of your comments and have added a multivariable Cox Regression analysis for pelvic control. We would have liked to include a multivariable model for local control as well. However, to reduce the risk of overfitting, we only performed a multivariable analysis for outcomes with >50 events. There were only 34 local recurrences in the entire cohort. Therefore, local control was only evaluated in a univariable analysis.

The variables selected for univariable analysis are based on previous literature and consensus among the co-authors (see lines 588-590). To reduce the risk of overfitting, the selection of variables for the multivariable model was based on p-value. However, as a result of your comments we have re-discussed our selection of variables (with an epidemiologist) and made some changes to the Cox regression analysis (Table 2).

Thank you for the interesting suggestion to include year of diagnosis as a covariate in the multivariable model. However, the three groups for different brachytherapy practices are also defined by treatment date. We have tried to explore this further by evaluating the log likelihood of the multivariable model with and without year of diagnosis (as a continuous variable). The log likelihood is 1477 without and 1476 with year of diagnosis in the model. Therefore, we do not expect the model to improve and have decided to omit this from the manuscript.

Point 3: Some results are difficult to understand since the methods section is not fully described. For illustration: It is tough to interpret the results from the Venn diagrams as your main outcomes were time-to-event variables, and it is not explicit in the methods why you present the results in this way. It is also unclear why toxicity was only provided as a frequency per treatment group when the other outcomes (tumor control, disease-free survival, and overall survival) were evaluated and modeled as time-to-event outcomes.

Response 3: We have included a Venn diagram in order to show the patterns of recurrence. These patterns are known from previous literature to differ between patients with high and low FIGO stage. Therefore, we performed stratification for patients with stage I-II and stage III-IV. This allows a more accurate comparison of recurrence patterns with previously published data. We have tried to address this issue in the manuscript, see lines 585-586.

As a result of the retrospective design of our study, we were not able to collect adequate time-to-event data for toxicity, as this is not always (correctly) reported in the medical records of the patients. We also reported the crude rate to compare our results with the retrospective EMBRACE study. As retrospective analysis of toxicity can lead to under-representation of toxicity, we only evaluated severe toxicity (grade 3 or higher). This is likely to be better specified in the medical records and therefore more reliable. We have elaborated on this in the manuscript on pages 1497 - 1502.

Point 4: As a minor suggestions, the authors should maintain consistency because it seems they are using 'local control', 'tumor control' and 'failure' to refer to the same concept. For instance, in Table 2, the first outcome is called 'local control'; in the methods, the outcome is defined as 'tumor control', but the title refers to 'failure'. So I guess the authors are referring to the time from diagnosis (local, pelvic, any) to recurrence. Additionally, many of the confounders were not described in the methods (WHO performance score, smoking, hypertension, etc.), and in my opinion, describing how the variables were measured provided insight into the quality of the study.

My suggestion would be to contact an epidemiologist and to ask for some support to analyze this interesting database.

Response 4: Thank you for your suggestions. We have removed several inconsistencies. For example, we have changed the title of Table 2 (Univariable and multivariable Cox regression analysis for local control, pelvic control, disease-free survival, and overall survival) and changed "brachytherapy techniques" to "brachytherapy practices" (to match the title). We also made several changes to the VENN diagram.

We asked an epidemiologist from our department to evaluate our current analysis. We made several changes to the Cox regression analysis (Table 2).

Reviewer 3 Report

The effect of contemporary brachytherapy practices on prognosis in women with locally advanced cervical cancer

 

In this report, the authors compare local control, pelvis control, progression free survival and overall survival between 3 cohort of patients (CT, MRI and MRI + needles) treated with external irradiation, followed by brachytherapy.

The CT group consisted of patients treated from October 2006 to September 2009. The field for external irradiation was defined based on CT images. The brachytherapy consisted of a single fraction with a dose-prescription of 24 Gy at point A.

Patients in the MRI group were treated September 2009 and January 2013.

MRI imaging was used to delineate the target for both EBRT and brachytherapy. Dosing was according to introduced GEC-ESTRO guidelines.

Patients in the MRI + needles group was treated after January 2013. During this period, MRI-guided adaptive brachytherapy combined with the use of parametrial interstitial needles was adapted.

Local control, pelvis control, progression free interval (PFS) and overall survival (OS) were used as endpoints. Severe late toxicity was registered. Local control, PFS and OS were significantly improved in the MRI + needles group compared to the CT group.

 

This is a well written report illustrating the improvements obtained with modern techniques for imaging combined with up-to-date radiation techniques in locally advanced cervical cancer.

The authors are to be congratulated with a well performed task.

Author Response

We are humbled and very grateful for the compliments from reviewer 3.

Reviewer 4 Report

I read with great interest the Manuscript titled "The effect of contemporary brachytherapy practices on prognosis in women with locally advanced cervical cancer" which falls within the aim of the Journal.

Although the manuscript can be considered already of high quality, I would suggest to take into account the following minor recommendations:

 

- I suggest another round of language revision, in order to correct few typos and improve readability.

-Inclusion/exclusion criteria should be better clarified by extending their description.

- Discussions can be expanded and improved by citing relevant articles about the risk of persistence/recurrence after primary conization (I suggest authors to read and insert in references the following article PMID: 35455328 and to Giannini, A.; Di Donato, V.; Sopracordevole, F.; Ciavattini, A.; Ghelardi, A.; Vizza, E; et al. Outcomes of High-Grade Cervical Dysplasia with Positive Margins and HPV Persistence after Cervical Conization. Vaccines 2023, 11, 698. https://doi.org/10.3390/vaccines11030698).

 

 

- The authors have not adequately highlighted the strengths and limitations of their study. I suggest better specifying these points.

 

Considered all these points, I think it could be of interest for the readers and, in my opinion, it deserves the priority to be published after minor revisions.

Author Response

Point 1: I suggest another round of language revision, in order to correct few typos and improve readability.

Response 1: In terms of spelling and sentence structure, we have made a number of adjustments and improvements throughout the manuscript.

Point 2: Inclusion/exclusion criteria should be better clarified by extending their description.

Response 2: The inclusion and exclusion criteria can indeed be made more explicit. We have dedicated the first paragraph of the Materials and methods section to the inclusion and exclusion criteria. We have also clarified which patients are eligible and which are excluded from the analysis. See the changes made in the manuscript on lines 97-100.

Point 3: Discussions can be expanded and improved by citing relevant articles about the risk of persistence/recurrence after primary conization (I suggest authors to read and insert in references the following article PMID: 35455328 and to Giannini, A.; Di Donato, V.; Sopracordevole, F.; Ciavattini, A.; Ghelardi, A.; Vizza, E; et al. Outcomes of High-Grade Cervical Dysplasia with Positive Margins and HPV Persistence after Cervical Conization. Vaccines 2023, 11, 698. https://doi.org/10.3390/vaccines11030698).

Response 3: Thank you for the reference to this interesting article. This study is based on cervical cancer patients with limited disease after surgery, and we cannot find ways to meaningfully translate or compare this to the patients in our study who have locally advanced disease and are treated with primary radiation therapy.

Point 4: The authors have not adequately highlighted the strengths and limitations of their study. I suggest better specifying these points.

Response 4: We agree and have made some changes to the discussion section and have devoted the last paragraph to our strengths and limitations (lines 1493-1506).

Considered all these points, I think it could be of interest for the readers and, in my opinion, it deserves the priority to be published after minor revisions.

Reviewer 5 Report

This article entitled, “The effect of contemporary brachytherapy practices on prognosis in women with locally advanced cervical cancer" demonstrated the efficacy of state-of-the-art MRI-guided adaptive brachytherapy combined with parametrial interstitial needles in women with locally advanced cervical cancer. The topic is interesting and the paper is well-written. I point out some major and minor flaws in this manuscript for the purpose of further improving the manuscript.

 

Major

1.     MRI+needles group included the patients with and without the interstitial brachytherapy. The authors should explain the indication criteria for interstitial brachytherapy.

2.     The authors demonstrated the treatment time was significantly difference among three groups in table 1. However, the treatment time was not evaluated in table 2. Previous reports indicated that longer treatment time of radiotherapy/concurrent chemoradiotherapy linked to unfavorable prognosis in the patients with cervical cancer. What are the authors’ thoughts on this?

 

Minor

1.     The authors described that higher age was one of the independent risk factors for overall survival. However, there was no definition of “higher age” in Table 2.

 

Author Response

Major:

Point 1: MRI+needles group included the patients with and without the interstitial brachytherapy. The authors should explain the indication criteria for interstitial brachytherapy.

Response 1: We are in agreement that this could be more explicit in the materials and methods and have made changes accordingly. See manuscript lines 360-365. The MRI+needles group represents patients with access to state-of-the-art MRI-guided adaptive brachytherapy with combined intracavitary/interstitial technique when needed. The use of these interstitial needles was optional, but was always indicated if suboptimal target coverage was expected or to better spare the organs at risk compared to the intracavitary only technique.

Point 2: The authors demonstrated the treatment time was significantly difference among three groups in table 1. However, the treatment time was not evaluated in table 2. Previous reports indicated that longer treatment time of radiotherapy/concurrent chemoradiotherapy linked to unfavorable prognosis in the patients with cervical cancer. What are the authors’ thoughts on this?

Response 2: This is a valid point, and we acknowledge that longer overall treatment time (generally greater than 50 days in the literature) is an important prognostic factor for our patient population. We have included overall treatment time in the Cox regression analysis (Table 2).

Minor:

Point 1: The authors described that higher age was one of the independent risk factors for overall survival. However, there was no definition of “higher age” in Table 2.

Response 1: We agree that both in the manuscript and in the table, the definition of age we used could be more explicit. Age at diagnosis (in years) was included as a continuous variable in the multivariable Cox regression analysis for overall survival. We have added this definition in the Methods section (see lines 328-329) and in Table 1 & 2. In addition, we have changed ‘age’ to ‘older age at diagnosis’ in line 32-33,  987-991.

 

Round 2

Reviewer 1 Report

none.

Reviewer 5 Report

Thank you for the revision. My concerns raised at the previous review have all been solved. I think the manuscript now deserves publication.