Attenuation of Immune Senescence Markers After Intensive Cancer Therapy Through Resistance Training: A Pilot Study

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The most suitable study design to assess the effect of an intervention would be a crossover, triple-blinded, randomized controlled trial, provided that this is ethically feasible and that the outcomes are not death or cure.

However, the effectiveness of a strength training program cannot be evaluated using a blinded design. In addition, including a control group of cancer survivors not receiving the intervention may raise ethical concerns. Therefore, a before-and-after study design appears to be the most appropriate option. Nevertheless, deviations from the randomized controlled trial design may introduce bias and confounding, which should be explicitly acknowledged and discussed in the manuscript.

Changes observed within this study design may be partly attributable to chance (given the small and specific group of cancer survivors), natural changes over time (including the effects of aging, co-morbidities, and time since last treatment), and secondary effects related to participation in a clinical trial (e.g., lifestyle changes such as diet, alcohol and tobacco consumption, sleep patterns, and sedentary behavior). A more detailed characterization of the recruitment process and of participant characteristics would help to better appraise the contribution of these factors.

Adherence to the training program may also have benefited from the fact that controls were partners of the cancer survivor participants. However, this arrangement may have introduced an additional emotional or motivational effect associated with performing the activity as a pair, which could have influenced the observed changes.

The introduction should more clearly present the concepts of aging and frailty in cancer survivors, noting that frailty may also be present in younger survivors. It should also address the clinical relevance of immune rejuvenation and describe how immune rejuvenation has been assessed in the existing literature. The research question, as well as the main and specific objectives, should be more explicitly stated in the final paragraph of the introduction.

Because not all cancer survivors are frail and frailty is part of the eligibility criteria, this characteristic should be consistently reflected when referring to the study population. For example, frailty should be explicitly mentioned in sentences such as:

• “We developed a community-based pilot study of resistance training for long-term cancer survivors”
• “We thus performed a community-based pilot study of strength training in long-term survivors of cancer, with a particular focus on allogeneic hematopoietic cell transplantation (HCT)”
• “In conclusion, our pilot study demonstrates that a community-based, personalized resistance training program is not only feasible for cancer survivors…”

Regarding participant selection, the authors are encouraged to clarify the following points:

• The use of the term “long-term cancer survivors” in light of the eligibility criterion stating that participants (N = 8) were required to be at least 18 months post-HCT or intensive multi-agent chemotherapy. In addition, the sentence “At the time of the study, all subjects were >1-year post-treatment” introduces ambiguity regarding the exact time since the last cancer treatment.
• The specific focus on allogeneic HCT recipients, given the statement that “the study was originally intended for allogeneic HCT recipients”.
• The low number of participants recruited over a relatively long inclusion period (2018–2019). How were participants identified and invited to participate? Who assessed frailty, and which criteria or tools were used to assess frailty in cancer survivors?

The sentence “Genes were considered differentially expressed if they had an adjusted p-value < 0.05 (Benjamini–Hochberg correction) and an absolute log2 fold-change ≥ 1, corresponding to at least a two-fold difference in expression” should be revised, as genes themselves do not have p-values; rather, statistical tests applied to gene expression data do.

In the Results section, interpretative statements and discussion of underlying mechanisms should be avoided. For example, the following sentences are more appropriate for the Discussion section and should be removed from Results:

• “The most enriched pathway from pre- to post-exercise was muscle catabolism…”
• “NAD and sirtuin pathways are often linked to cellular aging…”
• “Cancer-related genomic instability could reflect cellular stress response…”
• “The anabolic stimulus of resistance training may have contributed…”

Similarly, speculative interpretations regarding gut microbiome changes (e.g., increased stability or functional implications of specific taxa) should be relocated to the Discussion.

The quality of the images, particularly in Figure 5, is insufficient to allow adequate reading and interpretation and should be improved.

In the Discussion section, a first paragraph summarizing the main findings and directly addressing the objectives stated at the end of the introduction is missing and should be added.

In this pilot study, the small sample size limits the statistical power to detect differences in changes between groups. The absence of statistically significant differences may therefore be due to insufficient power rather than the absence of true effects, and this limitation should be explicitly acknowledged in the Discussion. For example, in Figure 6, the large dispersion of post-intervention values in the patient group likely contributes to the lack of statistically significant differences between groups after the training program.

Moreover, sex-related differences in aging-associated immune alterations have been reported (Mkhikian et al., 2022; McGill and Benayoun, 2022). As the study population included equal numbers of men and women, this factor may have contributed to increased variability in the results and should be discussed.

Finally, the reference list could be updated to reflect more recent literature.

 

 

 

 

 

Author Response

COMMENT: The most suitable study design to assess the effect of an intervention would be a crossover, triple-blinded, randomized controlled trial, provided that this is ethically feasible and that the outcomes are not death or cure. However, the effectiveness of a strength training program cannot be evaluated using a blinded design. In addition, including a control group of cancer survivors not receiving the intervention may raise ethical concerns. Therefore, a before-and-after study design appears to be the most appropriate option. Nevertheless, deviations from the randomized controlled trial design may introduce bias and confounding, which should be explicitly acknowledged and discussed in the manuscript.

RESPONSE: We appreciate the reviewer's thoughtful and methodologically rigorous assessment of the study design, and we are in full agreement with the core reasoning presented. As the reviewer notes, a crossover, triple-blinded, randomized controlled trial would represent the gold standard for evaluating an intervention of this nature; however, as the reviewer also acknowledges, such a design is neither practically feasible nor ethically appropriate in this context. Blinding participants to a resistance training intervention is inherently impossible, and withholding exercise from cancer survivors, particularly those meeting criteria for pre-frailty or frailty, would raise significant ethical concerns given the existing evidence supporting exercise in this population. We are grateful that the reviewer concurs that a before-and-after design is the most appropriate option for this type of investigation.

We wish to respectfully highlight that the manuscript, as currently written, frames the study explicitly and consistently as a pilot study, a designation that appears in the title, abstract, introduction, methods, results, and discussion, precisely to communicate that these findings are preliminary and hypothesis-generating rather than confirmatory.

 For example, in the Introduction, we state: "These preliminary data are useful to inform the development of a larger strength-focused longitudinal training program to reverse frailty and improve all possible domains of physiologic and social function after cancer therapy…" Similarly, in the Discussion, we acknowledge the early termination of the study and its implications:

"Unfortunately, our study was terminated before the target sample size was accrued due to the emergence of SARS-CoV2 as a public health threat, particularly among immunocompromised individuals. Nonetheless, our pilot study results are encouraging…"

And in the Conclusions:"Despite a small sample size, the consistency of gains across participants and the normalization of immune signatures suggest that resistance training may help reverse features of immune senescence… Larger, longitudinal studies are now needed to validate these findings…"

Additionally, throughout the manuscript we have been careful to employ hedged, hypothesis-generating language (e.g., "may reduce," "suggesting," "hypothesis-generating that resistance exercise could potentially exert a normalizing effect") rather than causal or definitive claims, specifically to reflect the limitations inherent in a non-randomized, unblinded pilot design.

That said, we appreciate the reviewer's suggestion that the potential for bias and confounding be explicitly named in the discussion. To address this, we propose adding a brief statement to the Discussion section's limitations paragraph, such as: "As a single-arm, non-randomized before-and-after pilot study without a non-exercising cancer survivor control group, the design is susceptible to potential biases and confounding, including selection bias, the absence of blinding, maturation effects, and the possibility that observed changes may reflect natural recovery, regression to the mean, or other temporal factors rather than the exercise intervention alone."

We believe this addition, while concise, directly addresses the reviewer's concern without overstating the limitations of what is already clearly framed as a hypothesis-generating pilot study. We trust the reviewer will agree that the manuscript's consistent pilot framing, cautious language, and calls for larger confirmatory trials collectively serve to contextualize the findings appropriately.

COMMENT:  Changes observed within this study design may be partly attributable to chance (given the small and specific group of cancer survivors), natural changes over time (including the effects of aging, co-morbidities, and time since last treatment), and secondary effects related to participation in a clinical trial (e.g., lifestyle changes such as diet, alcohol and tobacco consumption, sleep patterns, and sedentary behavior). A more detailed characterization of the recruitment process and of participant characteristics would help to better appraise the contribution of these factors.

RESPONSE: We thank the reviewer for this important and nuanced observation. The concerns raised are valid considerations in any before-and-after study design, and we agree they merit transparent discussion. We would like to address each of these potential confounders individually, highlight features of the study design and manuscript that already mitigate or account for several of these concerns, and describe the additions we propose to further strengthen the manuscript.

Regarding chance and small sample size: We fully agree that the small and specific cohort limits the generalizability of our findings and increases the possibility that some observed changes may be attributable to chance. As noted in our response to Comment 1, the manuscript is explicitly and consistently framed as a pilot study throughout and employs hedged, hypothesis-generating language precisely to reflect this limitation. We believe the statistical methods employed (including Benjamini-Hochberg correction for multiple testing in the genomic analyses) provide appropriate rigor for a study of this scope, but we readily acknowledge that confirmatory, adequately powered studies are needed. As stated in the Conclusions: "Larger, longitudinal studies are now needed to validate these findings and explore sustainable, scalable models for delivering strength-based interventions to cancer survivors in diverse settings."

Regarding natural changes over time: This is an important point, and we wish to draw the reviewer's attention to a key design feature that substantially mitigates this concern. All cancer survivors in our study were required to be at least 18 months post-HCT or intensive multi-agent chemotherapy at enrollment, as stated in Section 2.1: "Participants (N=8) were required to be at least 18 months post-HCT or intensive multi-agent chemotherapy." This eligibility criterion was intentionally chosen to select individuals well beyond the period of expected natural immunologic reconstitution and recovery, during which spontaneous improvement might be anticipated. In allogeneic HCT recipients, the most dynamic phase of immune reconstitution typically occurs within the first 12 months; by 18 months, the trajectory has generally plateaued. Thus, the likelihood that the immunologic changes we observed over a 10-week window reflect natural recovery or time-dependent reconstitution is substantially reduced, though admittedly not eliminated. Furthermore, participants were required to be on fewer than 20 mg of prednisone equivalent, reducing the likelihood that changes in immunosuppressive therapy during the study period could account for the observed findings. We also note that the healthy caregiver controls underwent the same intervention over the same time period, providing an internal comparator group exposed to the same environmental and temporal conditions. The fact that cancer survivors but not controls demonstrated significant transcriptomic and epigenetic changes suggests the findings are not simply explained by the passage of time or seasonal variation.

Regarding secondary effects of trial participation (lifestyle, diet, sleep, sedentary behavior): We appreciate this concern and would like to highlight several features of our study design that were specifically implemented to monitor or standardize these factors. As described in Section 2.1, all participants were provided with a Fitbit® device at study enrollment and encouraged to wear it throughout the study to track physical activity and sleep: "All participants were given a Fitbit® at the start of the study and encouraged to wear it as much as possible over the course of the study to allow tracking of activity and sleep." The Fitbit data are reported in Section 3.3 and provided in full in Supplemental Data, showing no statistically significant differences between cancer survivors and controls in accelerometer-derived metrics, including daily steps, active minutes, sleep duration, and heart rate. Regarding diet, as stated in Section 2.2: "No formal dietary intervention was implemented; however, a registered dietitian (JS) provided monthly group sessions focused on nutrition to support muscle growth." The absence of a formal dietary intervention and the standardized nature of the nutritional counseling (provided equally to all participants) reduce the likelihood that differential dietary changes account for the observed results. We acknowledge that alcohol consumption, tobacco use, and other lifestyle factors were not formally tracked, and this is a fair limitation to note.

Regarding recruitment process and participant characterization: We respectfully note that Table 1 provides baseline characteristics for all 16 participants, including group assignment, age, sex, treatment type, number of sessions completed, and inclusion in the genomics analysis. The eligibility criteria are detailed in Section 2.1, including disease and treatment requirements, frailty criteria, time from treatment, corticosteroid thresholds, and the requirement for a healthy exercise partner. We also describe the eligibility criteria during the study (also available on ClinicalTrials.gov) and the reason for early closure. To directly address the reviewer's request, we propose adding the following language to the Discussion section alongside the limitations statement proposed in our response to Comment 1: "Additionally, while all participants were at least 18 months post-treatment and the inclusion of healthy controls exposed to the same intervention and temporal conditions provides an internal comparator, we cannot fully exclude the contributions of natural physiologic changes over time, regression to the mean, or secondary behavioral effects of trial participation, such as changes in diet, alcohol or tobacco consumption, sleep, or sedentary behavior, to the observed outcomes. Fitbit-derived activity and sleep data did not differ significantly between groups and are provided in Supplemental Data, and nutritional counseling was standardized across all participants; however, not all lifestyle variables were formally monitored.”

We believe this addition, in combination with the existing pilot framing, eligibility criteria, and Fitbit monitoring, comprehensively addresses the reviewer's concerns while maintaining an accurate representation of the study's strengths and limitations.

COMMENT:  Adherence to the training program may also have benefited from the fact that controls were partners of the cancer survivor participants. However, this arrangement may have introduced an additional emotional or motivational effect associated with performing the activity as a pair, which could have influenced the observed changes.

RESPONSE: We thank the reviewer for raising this thoughtful point, and we agree that the pairing of cancer survivors with their caregivers represents both a deliberate design strength and a potential source of confounding that merits transparent discussion. We wish to respectfully highlight that this dynamic was not an unintended consequence of our recruitment strategy but rather a purposeful design feature of the study, and its implications are already discussed in the manuscript. Specifically, in the Discussion section, we state: "Pairing cancer survivors with healthy caregivers may have further supported adherence and engagement, while also acknowledging the impact of cancer on caregivers and promoting healthier family-level behaviors."

This design choice was motivated by several interrelated considerations rooted in the realities of exercise programming for medically complex populations. First, from a feasibility and adherence standpoint, community-based exercise interventions in cancer survivors are frequently limited by high attrition rates, and the inclusion of a familiar exercise partner was intended to provide built-in social accountability, reduce barriers to attendance, and foster a sense of shared purpose, all of which are well-recognized facilitators of exercise adherence in the behavioral science literature. Second, from a clinical and humanistic standpoint, the burden of cancer and its treatment extends well beyond the patient to caregivers, who themselves are at increased risk for physical deconditioning, psychological distress, and adverse health outcomes. By including caregivers as active participants rather than passive bystanders, the study design acknowledged this broader impact and offered a tangible health benefit to the caregiver population as well. Third, from a scientific standpoint, the use of caregivers as controls provided a comparator group that shared the same environmental exposures, temporal conditions, group training sessions, and nutritional counseling as the cancer survivors, thereby controlling for many of the non-specific trial participation effects raised by the reviewer in the preceding comment.

That said, we fully agree with the reviewer that this arrangement may have introduced an additional emotional or motivational effect that could have influenced adherence, effort, or even psychosocial well-being, any of which could in turn have contributed to the physiologic changes observed. This is a legitimate consideration, and we acknowledge that it is not possible to fully disentangle the immunologic and epigenetic effects of the resistance training stimulus itself from the potential psychosocial benefits of exercising alongside a supportive partner. However, we would note that this concern applies symmetrically to both groups and therefore the motivational effect of paired participation would not be expected to differentially bias the between-group comparisons that form the basis of our key immunologic findings (i.e., the normalization of transcriptomic and epigenetic differences between cancer survivors and controls post-exercise). If anything, a shared motivational boost would be expected to enhance outcomes in both groups comparably, making the finding that cancer survivors exhibited significant transcriptomic and epigenetic changes all the more notable. To address this comment directly, we propose adding a brief acknowledgment to the Discussion section within the limitations paragraph: "The pairing of cancer survivors with their caregivers, while intentionally designed to support adherence and provide a shared-exposure control group, may have introduced an additional emotional or motivational effect inherent to exercising as a dyad, which cannot be fully separated from the effects of the training intervention itself."

We believe this concise addition, in combination with the existing discussion of the caregiver-pairing rationale already present in the manuscript, appropriately addresses the reviewer's concern without overstating the limitation, particularly given that the partner effect would be expected to operate symmetrically across both groups.

COMMENT:  The introduction should more clearly present the concepts of aging and frailty in cancer survivors, noting that frailty may also be present in younger survivors. It should also address the clinical relevance of immune rejuvenation and describe how immune rejuvenation has been assessed in the existing literature. The research question, as well as the main and specific objectives, should be more explicitly stated in the final paragraph of the introduction.

RESPONSE: We thank the reviewer for these suggestions regarding the structure and content of the Introduction. Regarding aging and frailty in cancer survivors, including younger survivors: We respectfully note that the Introduction already devotes substantial attention to the concepts of aging and frailty in cancer survivors. The opening paragraph explicitly establishes that "Cancer therapy can accelerate aging of multiple physiologic systems, resulting in an increased risk of frailty, a clinical syndrome of diminished physiologic reserve and low resistance to stressors," followed by a description of frailty manifestations (weakness, low physical activity, exercise intolerance, unintentional weight loss, self-reported exhaustion, and low self-efficacy) with reference to the Fried et al. criteria. We further state that "frailty is likely underdiagnosed in cancer survivors" and emphasize the need to "increase the recognition of the effects of cancer diagnosis as well as cancer therapy that exert deleterious effects on the hallmarks of aging." Importantly, this language is deliberately not age-restricted — the term "cancer survivors" is used throughout without qualification to an elderly population, and the cited references (including Arora et al., Hurria et al., and Sedrak et al.) collectively address frailty across the age spectrum in cancer populations. That said, we recognize the value of making the point about younger survivors more explicit and propose adding a brief clause to the first paragraph: "Notably, therapy-induced frailty is not limited to older adults; younger cancer survivors, including recipients of hematopoietic cell transplantation, may also develop features of accelerated physiologic aging."

Regarding the clinical relevance of immune rejuvenation and its assessment in existing literature: We appreciate this suggestion. We note that the Discussion section currently provides context on immune rejuvenation and immunosenescence, citing a preclinical mouse model demonstrating that exercise reversed age-induced changes in gene expression (Liu et al., reference 29), as well as studies examining the influence of exercise on immunosenescence during aging (references 30–33) and a large meta-analysis showing that exercise reduces proinflammatory markers in cancer survivors (reference 34). We also reference the landmark NEJM randomized trial demonstrating a disease-free survival benefit of structured exercise in colon cancer (Courneya et al., reference 13). While we understand the reviewer's preference for this context to appear in the Introduction, we respectfully submit that the Introduction as currently structured follows a conventional and logical flow: establishing the clinical problem (frailty and accelerated aging), presenting the proposed intervention (resistance training), summarizing existing evidence for exercise in relevant populations, and then stating the rationale for the current study. Relocating the detailed discussion of immune rejuvenation assessment methods and prior literature into the Introduction would, in our view, risk front-loading the manuscript with extensive background that is more appropriately situated in the Discussion, where it can be interpreted in the context of our findings.

We respectfully note that the final paragraph of the Introduction does articulate the study's purpose and scope.

COMMENT:  Because not all cancer survivors are frail and frailty is part of the eligibility criteria, this characteristic should be consistently reflected when referring to the study population. For example, frailty should be explicitly mentioned in sentences such as:

• “We developed a community-based pilot study of resistance training for long-term cancer survivors”
• “We thus performed a community-based pilot study of strength training in long-term survivors of cancer, with a particular focus on allogeneic hematopoietic cell transplantation (HCT)”
• “In conclusion, our pilot study demonstrates that a community-based, personalized resistance training program is not only feasible for cancer survivors…”

RESPONSE: We thank the reviewer for this observation and agree that the frailty criterion is a defining and important feature of our study population. We would like to respectfully highlight, however, that this characteristic is already prominently and explicitly established in the manuscript in the locations where it is most methodologically appropriate — and that appending frailty qualifiers to every mention of the study population throughout the text may introduce unnecessary redundancy without meaningfully enhancing clarity. Specifically, frailty as an eligibility criterion is clearly stated in Section 2.1 (Patients and Methods), which reads: "Participants (N=8) were required to be at least 18 months post-HCT or intensive multi-agent chemotherapy, meet criteria for pre-frailty or frailty per Fried et al criteria (all had low energy expenditure and self-reported exhaustion), and have a healthy exercise partner (caregiver, spouse, other relative, or friend) who could serve as a control."

This passage unambiguously establishes that every cancer survivor enrolled met Fried criteria for pre-frailty or frailty, and it does so at the point in the manuscript where eligibility criteria are conventionally reported. Once this criterion is clearly defined in the Methods, the reader carries this understanding forward through the Results, Discussion, and Conclusions. Indeed, the entire first paragraph of the Introduction is devoted to establishing the relationship between cancer therapy, accelerated aging, and frailty, including the clinical manifestations of frailty, its underdiagnosis in cancer survivors, and the unmet need to address it, such that by the time the reader encounters the study description, the frailty context is already firmly established. Furthermore, we note that the three sentences the reviewer has identified serve different rhetorical functions and, in each case, the surrounding context (eligibility criteria in the Methods, frailty discussion in the Introduction, and the overall framing of the paper) makes it clear that the population studied consisted of pre-frail or frail cancer survivors. Modifying each of these sentences to include qualifiers such as "pre-frail or frail" would, in our view, make the prose cumbersome, particularly in the Abstract where brevity is paramount.

That said, we recognize the reviewer's underlying concern that a reader encountering any single section in isolation should understand that this was a study of cancer survivors meeting frailty criteria, not cancer survivors generally. As a compromise, we propose one addition to the Abstract, where the population is first introduced and where stand-alone readability is most important, by modifying the sentence to read: "We developed a community-based pilot study of resistance training for long-term cancer survivors meeting criteria for pre-frailty or frailty (N=8; 6 allogeneic hematopoietic cell transplant, 1 autologous hematopoietic transplant, 1 breast cancer survivor) and their caregivers (N=8 healthy controls)…" We believe this single, targeted addition, combined with the detailed eligibility criteria in Section 2.1 and the extensive frailty discussion in the Introduction, ensures that the frailty characteristic of the study population is unmistakably clear to any reader.

COMMENT;  Regarding participant selection, the authors are encouraged to clarify the following points:

• The use of the term “long-term cancer survivors” in light of the eligibility criterion stating that participants (N = 8) were required to be at least 18 months post-HCT or intensive multi-agent chemotherapy. In addition, the sentence “At the time of the study, all subjects were >1-year post-treatment” introduces ambiguity regarding the exact time since the last cancer treatment.
• The specific focus on allogeneic HCT recipients, given the statement that “the study was originally intended for allogeneic HCT recipients”.
• The low number of participants recruited over a relatively long inclusion period (2018–2019). How were participants identified and invited to participate? Who assessed frailty, and which criteria or tools were used to assess frailty in cancer survivors?

RESPONSE: We thank the reviewer for these detailed questions regarding participant selection and recruitment. We will address each sub-point individually and highlight where the manuscript already provides the requested information. Regarding the term "long-term cancer survivors" and the time-since-treatment criterion: We appreciate the reviewer's attention to terminology. The eligibility criterion stated in Section 2.1 specifies that participants were required to be "at least 18 months post-HCT or intensive multi-agent chemotherapy." The subsequent sentence stating that "all subjects were >1-year post-treatment" was intended as a general contextual statement reflecting that all participants were well beyond the acute treatment and early recovery phase; however, we acknowledge that juxtaposing the 18-month eligibility requirement with a ">1-year" statement could introduce ambiguity. To resolve this, we revised the latter sentence to align precisely with the eligibility criterion: "At the time of the study, all subjects were at least 18 months post-treatment and were receiving <20 mg of prednisone/equivalent."

This minor revision eliminates any inconsistency between the two statements. Regarding the use of "long-term cancer survivors," we respectfully note that this term is widely used in the survivorship literature to describe individuals who have completed active cancer treatment and are in the post-treatment phase, and the 18-month minimum post-treatment requirement comfortably places our participants within this category. We are, however, open to the reviewer's or editor's preference if an alternative term is felt to be more precise.

Regarding the specific focus on allogeneic HCT recipients: As described in Section 2.1, the study was originally designed for allogeneic HCT recipients, a population that undergoes high-dose conditioning chemotherapy followed by donor stem cell infusion and subsequent immune reconstitution, making them a uniquely informative population in which to study the intersection of cancer therapy, immune senescence, and exercise-mediated immune restoration. The manuscript transparently states:

"The study was originally intended for allogeneic HCT recipients but given preliminary benefits with the first cohort of 4 patients, we expanded eligibility to anyone who had received intensive chemotherapy."

This expansion was a pragmatic decision made after the first cohort demonstrated encouraging results and was intended to broaden the applicability of the findings and improve enrollment. We believe the manuscript is transparent about this evolution in eligibility criteria. The rationale for the initial focus on allogeneic HCT is further supported in the Introduction, which states: "We thus performed a community-based pilot study of strength training in long-term survivors of cancer, with a particular focus on allogeneic hematopoietic cell transplantation (HCT)." And in the Discussion: "While we intended to recruit a broad range of patients, due to the timing of the study, we recruited mainly recipients of hematopoietic cell transplantation, who are exposed to high-dose chemotherapy and receive stem cells that reconstitute the immune system. This skewing of our population may have contributed to the results indicating resolution of inflammation and restoration of naïve T cell generation." We believe these passages collectively provide a clear and candid account of the population focus, the rationale for it, and its potential influence on the results.

Regarding the number of participants and the recruitment period: We appreciate the opportunity to provide additional context here. The study enrolled participants in two sequential cohorts of four cancer survivor–caregiver pairs each (i.e., 4 patients and 4 controls per cohort), which is a practical and common approach for community-based exercise interventions that involve supervised group training sessions. The first cohort was enrolled and completed the program, and upon observing preliminary benefits, the second cohort was enrolled with expanded eligibility criteria. The study was then closed to further enrollment due to the emergence of the COVID-19 pandemic, which posed unacceptable risks to immunocompromised participants in shared gym settings. This is stated in the manuscript: "The study was closed to new enrollment early given the challenges the COVID19 pandemic posed to safe gym access for immunocompromised individuals." The enrollment period of 2018–2019 therefore reflects the time required to sequentially run two cohorts through the full 10-week intervention prior to the pandemic-related closure, rather than a prolonged period of low recruitment yield.

Regarding how participants were identified and invited, the study recruited from the hematopoietic cell transplant and oncology clinics at the University of Minnesota through clinician referral and patient self-referral. Frailty was assessed by the study team using the Fried et al. criteria, as explicitly stated in Section 2.1: "meet criteria for pre-frailty or frailty per Fried et al criteria (all had low energy expenditure and self-reported exhaustion)." The Fried frailty phenotype is among the most widely used and validated tools for assessing frailty in both general and oncologic populations, and the specific domains met by our participants (low energy expenditure and self-reported exhaustion) are clearly documented.

COMMENT:  The sentence “Genes were considered differentially expressed if they had an adjusted p-value < 0.05 (Benjamini–Hochberg correction) and an absolute log2 fold-change ≥ 1, corresponding to at least a two-fold difference in expression” should be revised, as genes themselves do not have p-values; rather, statistical tests applied to gene expression data do.

RESPONSE: We thank the reviewer for this observation regarding statistical language precision. The reviewer is technically correct that p-values are properties of statistical tests applied to gene expression data rather than intrinsic properties of genes themselves, and we appreciate the attention to methodological rigor in scientific writing. We would respectfully note that the phrasing used in our manuscript is a widely adopted convention in the genomics and bioinformatics literature and appears routinely in high-impact publications describing RNA sequencing and differential expression analyses. This shorthand is generally understood by readers in the field to mean that the statistical test applied to each gene's expression data yielded an adjusted p-value below the stated threshold. Nonetheless, we recognize the reviewer's point that greater precision would enhance clarity, particularly for readers from other disciplines. We propose revised the sentence to read: "Genes were considered differentially expressed if the corresponding statistical test yielded an adjusted p-value < 0.05 (Benjamini–Hochberg correction) and an absolute log2 fold-change ≥ 1, corresponding to at least a two-fold difference in expression." We believe this revision preserves the readability and flow of the original sentence while addressing the reviewer's valid concern about attributing statistical properties to genes rather than to the tests applied to their expression data.

COMMENT:  In the Results section, interpretative statements and discussion of underlying mechanisms should be avoided. For example, the following sentences are more appropriate for the Discussion section and should be removed from Results:

• “The most enriched pathway from pre- to post-exercise was muscle catabolism…”
• “NAD and sirtuin pathways are often linked to cellular aging…”
• “Cancer-related genomic instability could reflect cellular stress response…”
• “The anabolic stimulus of resistance training may have contributed…”

RESPONSE: We thank the reviewer for this guidance regarding the separation of results from interpretation, which is an important principle of scientific writing that we have endeavored to uphold throughout the manuscript. We wish to respectfully inform the reviewer that the majority of the specific sentences cited in this comment have already been removed from the manuscript during a prior round of revision at the request of a previous reviewer who raised a similar concern. Specifically, the following phrases identified by the reviewer are no longer present in the current version of the Results section:

"NAD and sirtuin pathways are often linked to cellular aging…"

"Cancer-related genomic instability could reflect cellular stress response…"

"The anabolic stimulus of resistance training may have contributed…"

These interpretive statements were recognized as more appropriate for the Discussion and were removed accordingly in our prior revision. Regarding the remaining sentence identified by the reviewer  ("The most enriched pathway from pre- to post-exercise was muscle catabolism; NAD, sirtuins and aging was also present in the top enriched pathways") we respectfully submit that this sentence, as currently written, is descriptive rather than interpretive. It reports the factual output of the Enrichr® pathway enrichment analysis (Table 3) by identifying the top-ranked pathways by name, in the same manner that one might state "the most significantly enriched pathway was the interferon gamma response" in Section 3.4.1. The sentence does not speculate on mechanisms, attribute causality, or discuss the biological significance of these pathways. It simply names them as results of the analysis. We note that pathway enrichment results are conventionally reported in this manner in the genomics literature, where identifying and naming the top enriched pathways is considered part of the results rather than interpretation. We would further note that removing this sentence would leave the reader without any narrative description of the pathway analysis results presented in Table 3, requiring them to interpret the table entirely without guidance.

We are, of course, willing to further modify this sentence if the reviewer feels strongly that any element remains interpretive.

COMMENT: Similarly, speculative interpretations regarding gut microbiome changes (e.g., increased stability or functional implications of specific taxa) should be relocated to the Discussion.

The quality of the images, particularly in Figure 5, is insufficient to allow adequate reading and interpretation and should be improved.

RESPONSE: We thank the reviewer for these two points, which we will address in turn. Regarding speculative interpretations of gut microbiome changes in the Results section: We appreciate the reviewer's continued attention to maintaining a clear boundary between results and interpretation, and we have carefully re-examined Section 3.6 with this concern in mind. We acknowledge that a small number of sentences in this section contain language that extends modestly beyond purely descriptive reporting. However, we would respectfully note that in microbiome research, it is common and often necessary to provide brief contextual annotations alongside compositional findings, particularly when reporting individual-level changes in taxa or pathway abundances, so that the reader can follow the biological relevance of otherwise unfamiliar microbial names and pathway designations. Presenting species names and pathway shifts without any orienting context risks rendering the Results section opaque to the non-specialist reader. Regarding figure quality: We appreciate the reviewer's note regarding image quality. We wish to clarify that the figures currently in the manuscript were uploaded in high resolution; however, it is possible that image compression during the manuscript submission or PDF rendering process may have reduced their quality. Upon manuscript acceptance, we will work with the journal to ensure that the figures are suitable for publication.

COMMENT:   In the Discussion section, a first paragraph summarizing the main findings and directly addressing the objectives stated at the end of the introduction is missing and should be added.

In this pilot study, the small sample size limits the statistical power to detect differences in changes between groups. The absence of statistically significant differences may therefore be due to insufficient power rather than the absence of true effects, and this limitation should be explicitly acknowledged in the Discussion. For example, in Figure 6, the large dispersion of post-intervention values in the patient group likely contributes to the lack of statistically significant differences between groups after the training program.

RESPONSE: Regarding an opening summary paragraph in the Discussion: We acknowledge that the Discussion section, as currently written, moves directly into contextual framing and interpretation without first providing a concise recapitulation of the principal findings. While we note that the Abstract already provides a complete summary of the main results and that the Conclusions section synthesizes the key takeaways, we agree that an opening summary paragraph in the Discussion is a common and reader-friendly convention that would improve the section's structure. We propose adding the following paragraph at the beginning of the Discussion:

"In this community-based pilot study of pre-frail or frail cancer survivors and their healthy caregiver controls, a 10-week personalized resistance training program was feasible, safe, and associated with meaningful improvements across multiple domains. Both cancer survivors and controls more than doubled their training volume, with no serious adverse events. Cancer survivors exhibited favorable changes in body composition, including reductions in body fat percentage and fat mass with preservation or gain of lean mass. At the transcriptomic level, cancer survivors demonstrated a pro-inflammatory, immunosenescent gene expression profile at baseline, characterized by elevated interferon signaling and reduced naïve T cell signatures, that was no longer significantly different from healthy controls after the intervention. Similarly, epigenetic differences between groups, particularly in genes related to naïve T cell biology, normalized after resistance training, and pathway analysis revealed exercise-associated hypomethylation of innate immune and Toll-like receptor genes in cancer survivors. Gut microbiome pathway differences present at baseline were also no longer statistically significant post-exercise. Taken together, these findings suggest that resistance training may exert anti-inflammatory and immune-restorative effects in cancer survivors beyond the well-established musculoskeletal benefits."

We believe this paragraph directly addresses the study's objectives, evaluating the feasibility and effects of resistance training on strength, body composition, and immune-related biomarkers, and provides the reader with a clear overview of the principal findings before the subsequent interpretive discussion. Importantly, this is a new addition that does not require modification or relocation of any existing text.

Regarding statistical power and the interpretation of non-significant differences: We fully agree with the reviewer that the small sample size of our pilot study limits statistical power and that the absence of statistically significant differences in certain comparisons should not be interpreted as evidence of no effect. This is a fundamental distinction (absence of evidence versus evidence of absence) that is particularly important in pilot studies, and we appreciate the reviewer's emphasis on this point.

We respectfully note that the manuscript already addresses the small sample size limitation in multiple locations. The Conclusions state: "Despite a small sample size, the consistency of gains across participants and the normalization of immune signatures suggest that resistance training may help reverse features of immune senescence…" And the Discussion acknowledges the early termination of the study: "Unfortunately, our study was terminated before the target sample size was accrued due to the emergence of SARS-CoV2 as a public health threat." The consistent designation of the study as a "pilot" throughout the manuscript is itself an acknowledgment that the study was not powered to detect definitive between-group differences but rather to generate preliminary evidence and inform future trial design.

COMMENT: Moreover, sex-related differences in aging-associated immune alterations have been reported (Mkhikian et al., 2022; McGill and Benayoun, 2022). As the study population included equal numbers of men and women, this factor may have contributed to increased variability in the results and should be discussed.

RESPONSE: This is an important area of investigation that merits attention in appropriately designed and powered studies. However, we respectfully submit that a detailed discussion of sex-related differences in immunosenescence is beyond the scope of what can be meaningfully addressed in the current manuscript. With a small sample size, any attempt to analyze or interpret sex-stratified immune, epigenetic, or microbiome outcomes would be profoundly underpowered and at substantial risk of generating misleading conclusions. Presenting such analyses or speculating about their implications in a study of this size could paradoxically introduce the very type of overinterpretation that the reviewer has appropriately cautioned against in earlier comments regarding the Results section.

We believe that introducing a discussion of sex-specific immune aging in a 16-participant pilot study would risk overstating the interpretive reach of our data and extend the Discussion into territory that is more appropriately explored in the larger, adequately powered studies that we call for in the Conclusions: "Larger, longitudinal studies are now needed to validate these findings and explore sustainable, scalable models for delivering strength-based interventions to cancer survivors in diverse settings." Future studies with sufficient sample sizes to support sex-stratified analyses will be essential to address this important question, and we are grateful to the reviewer for highlighting it as a consideration for future work.

COMMENT: Finally, the reference list could be updated to reflect more recent literature.

RESPONSE: We respectfully submit that the reference list, as currently compiled, already reflects a substantial body of recent literature. Of the 41 references cited in the manuscript, a considerable proportion were published within the last several years, and numerous references were published in 2025 alone.  Additionally, seminal references that are older, such as Fried et al. (2001) for the frailty phenotype definition, or for the foundational bioinformatics tools (edgeR, DESeq2, limma) used in our analyses, are necessarily retained because they represent the original descriptions of criteria, tools, and methods that are integral to the study. Replacing these with more recent publications would be methodologically inappropriate.

Reviewer 2 Report

Comments and Suggestions for Authors

Newell and colleagues present an interesting study about the benefits of exercise in cancer patients. Their data suggests that strength training induces positive changes with respect to DNA methylation regions and pro-inflammatory profile in cancer survivors.

Major Revisions:

I would recommend the authors to reorganize their data to make the manuscript more impactful. Figure 1 compares weight, lean body mass, fat mass, ECW and other parameters and shows no significant difference between the patient and control cohort. Similarly, Figure 2 depicting the percent change in training volume does not indicate any difference.  The actual differences are seen in the RNA seq, DNA methylation and the Gut microbiome composition data. I strongly recommend starting the manuscript with these data. Re-arranging the data can emphasize that the changes observed in the cancer patients pertain more so to the cancer-induced inflammatory profile and other parameters are not impacted. Alternatively, they need to strengthen their writing to emphasize the significance of their initial data (Figures 1 and 2).

 

Second, the authors chose five of the patients and controls who exercised the most for their analysis. The inclusion of the remaining 3 personnel from both patient and control cohort would have helped determine the changes induced by exercise, particularly in patients who exercised more compared to those who did at the basal levels.

 

Minore revisions:

1. Line 99: The authors mentioned that the first cohort had 4 patients, and later they included additional patients. Please clarify if, in the data shown, all the patients received strength training for the same time period (10 weeks)?
2. In this cohort, was there a difference in patients who exercised more often as compared to patients who did the basal levels?
3. It will be helpful to present Figure 4 in a graphical format.

 

Author Response

COMMENT: Major Revisions:

I would recommend the authors to reorganize their data to make the manuscript more impactful. Figure 1 compares weight, lean body mass, fat mass, ECW and other parameters and shows no significant difference between the patient and control cohort. Similarly, Figure 2 depicting the percent change in training volume does not indicate any difference.  The actual differences are seen in the RNA seq, DNA methylation and the Gut microbiome composition data. I strongly recommend starting the manuscript with these data. Re-arranging the data can emphasize that the changes observed in the cancer patients pertain more so to the cancer-induced inflammatory profile and other parameters are not impacted. Alternatively, they need to strengthen their writing to emphasize the significance of their initial data (Figures 1 and 2).

RESPOSNE: We appreciate the reviewer's feedback and agree. We have moved the biometric and resistance training outcomes to supplemental data so that the reader can more clearly focus on the unique biological findings this analysis offers. Corresponding updates to the manuscript can be found in red in the revised document.

COMMENT: Second, the authors chose five of the patients and controls who exercised the most for their analysis. The inclusion of the remaining 3 personnel from both patient and control cohort would have helped determine the changes induced by exercise, particularly in patients who exercised more compared to those who did at the basal levels.

RESPOSNE: We agree with this concept. However, due to limited funding for correlative studies, we had to be selective about our experimental design. Our results are hypothesis generating and will ultimately need to be confirmed in larger controlled studies.

Minor revisions:

COMMENT: Line 99: The authors mentioned that the first cohort had 4 patients, and later they included additional patients. Please clarify if, in the data shown, all the patients received strength training for the same time period (10 weeks)?

RESPOSNE: Correct, patients and controls were recruited in pairs of 4. All enrolled participants received strength training for 10 weeks regardless of when they were enrolled.

COMMENT: In this cohort, was there a difference in patients who exercised more often as compared to patients who did the basal levels?

RESPOSNE: We could not determine a difference given the small sample size of this pilot study. This important question will need to be confirmed in larger studies.

COMMENT: It will be helpful to present Figure 4 in a graphical format.

RESPOSNE: We reviewed the different graphical options that Enrichr offers and ultimately felt this bar graph was able to show most clearly the magnitude of changes in pathways from pre-exercise to post-exercise in recipients. Thus, we retained this bar graph.

Reviewer 3 Report

Comments and Suggestions for Authors

This manuscript addresses an interesting and timely problem - whether resistance training can improve immune system functions in patients following anti-cancer treatment. The authors should be congratulated on the extent of analyses conducted within this small, pilot study. 

Major concerns:
1. The title is inaccurate and should be revised.

First, the term "radiation" is never described, quantified, or analyzed anywhere in the text. There is no information about which participants received radiotherapy, what anatomical sites were irradiated (local irradiation?, TBI?). This is a significant inconsistency that misrepresents the study population and should be corrected.

Second, the term "immune rejuvenation" overstates what the data actually demonstrate. The study shows normalization of transcriptomic and epigenetic differences between cancer survivors and healthy controls, and attenuation of pro-inflammatory pathway signatures. However it is not equal to rejuvenation, which implies an active reversal toward a younger immune state. Moreover, there were no direct measures of immune function; the genomic analyses were limited to 5 matched pairs, and the durability of the observed changes beyond 10 weeks is entirely unknown. The changes observed may reflect reduced inflammation rather than true immune restoration.
A more accurate and appropriately measured title would be: "Attenuation of immune senescence markers after intensive cancer therapy through resistance training: a pilot study." This formulation removes the unsupported reference to radiation, replaces the overclaim of "rejuvenation" and accurately reflects the mixed-therapy cohort, and signals the preliminary nature of the findings.

2. Speculative language in the Results section. On several occasions, interpretive and speculative statements appear within the Results rather than the Discussion, where they belong. For example, statements attributing observed pathway changes to "inactivity, systemic inflammation, aging, or underlying disease," or suggesting that mTORC1 elevation "may reflect an attempt at anabolic compensation," represent hypothesis-generating commentary that should be reserved for the Discussion. Results should report findings; their mechanistic interpretation belongs elsewhere.

Summary:
This is an interesting and methodologically rich pilot study on an important topic. However, the inaccurate and overclaiming title, the very small and heterogeneous study population, and the encroachment of speculative interpretation into the Results section all require revision before publication. The authors should frame their findings consistently as hypothesis-generating throughout, in keeping with the constraints of a small pilot study.

Author Response

COMMENT: The title is inaccurate and should be revised. First, the term "radiation" is never described, quantified, or analyzed anywhere in the text. There is no information about which participants received radiotherapy, what anatomical sites were irradiated (local irradiation?, TBI?). This is a significant inconsistency that misrepresents the study population and should be corrected. Second, the term "immune rejuvenation" overstates what the data actually demonstrate. The study shows normalization of transcriptomic and epigenetic differences between cancer survivors and healthy controls, and attenuation of pro-inflammatory pathway signatures. However it is not equal to rejuvenation, which implies an active reversal toward a younger immune state. Moreover, there were no direct measures of immune function; the genomic analyses were limited to 5 matched pairs, and the durability of the observed changes beyond 10 weeks is entirely unknown. The changes observed may reflect reduced inflammation rather than true immune restoration. A more accurate and appropriately measured title would be: "Attenuation of immune senescence markers after intensive cancer therapy through resistance training: a pilot study." This formulation removes the unsupported reference to radiation, replaces the overclaim of "rejuvenation" and accurately reflects the mixed-therapy cohort, and signals the preliminary nature of the findings.

RESPONSE: We understand and appreciate this reviewer's thoughtful comments. We have revised the title accordingly and eliminated claims of rejuvenation or other potential overstatements, focusing on hypothesis generation, throughout the manuscript. Additions to the manuscript can be found in red text throughout.

COMMENT: Speculative language in the Results section. On several occasions, interpretive and speculative statements appear within the Results rather than the Discussion, where they belong. For example, statements attributing observed pathway changes to "inactivity, systemic inflammation, aging, or underlying disease," or suggesting that mTORC1 elevation "may reflect an attempt at anabolic compensation," represent hypothesis-generating commentary that should be reserved for the Discussion. Results should report findings; their mechanistic interpretation belongs elsewhere.

RESPONSE: We agree and have deleted unhelpful or misplaced editorial/contextual remarks from the Results section.

COMMENT: Summary:
This is an interesting and methodologically rich pilot study on an important topic. However, the inaccurate and overclaiming title, the very small and heterogeneous study population, and the encroachment of speculative interpretation into the Results section all require revision before publication. The authors should frame their findings consistently as hypothesis-generating throughout, in keeping with the constraints of a small pilot study.

RESPONSE: We are grateful for your review and recognition of the potential contribution of this pilot study to the body of literature exploring physiologic benefits of exercise. We have revised our manuscript according to your guidance and emphasize throughout that this report is intended to be hypothesis-generating. Our results will need to be confirmed in larger, controlled studies.

 

 

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

Hi,

The authors have addressed my concerns and I recommend accepting this revised manuscript.

Best wishes.