Treatment of Leukemic Blood Samples with Granulocyte-Macrophage-Colony-Stimulating-Factor Combined with Prostaglandin E1 Is Associated with Reduced Frequencies of Tolerogenic Dendritic Cells and Increased Cytotoxicity Against Autologous Blasts

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

This study evaluates the effect of Kit-M (GM-CSF combined with PGE1) on the immune microenvironment of acute myeloid leukemia samples. The authors report that Kit-M treatment reduces the frequency of tolerogenic dendritic cells while promoting leukemia-derived dendritic cells, correlating with enhanced T-cell mediated antileukemic cytotoxicity. The study addresses a relevant clinical need—reversing immune evasion in AML—and benefits from a paired experimental design using whole blood rather than isolated PBMCs, which better captures the complexity of the leukemic niche. However, several methodological and interpretative limitations currently prevent acceptance.

Major Issues Requiring Correction

The most critical flaw concerns the claim of antileukemic specificity. Throughout the manuscript, the authors describe the observed immune responses as "leukemia-specific," yet the cytotoxicity assay uses only autologous blasts as targets without any control targets such as autologous non-leukemic cells or allogeneic blasts. This design cannot distinguish between genuine T-cell receptor mediated recognition of leukemia-associated antigens and non-specific killing mediated by natural killer cells or other innate effectors. Until specificity controls or blocking experiments are included, this claim remains unsubstantiated.

A second major issue is the lack of functional proof for the proposed mechanistic role of tolerogenic dendritic cells. The authors demonstrate a significant negative correlation between reduced tolerogenic dendritic cell frequencies and improved blast lysis, and they interpret this as evidence that Kit-M enhances immunity by reducing tolerogenic subsets. However, correlation does not establish causation. The authors have not directly tested whether tolerogenic dendritic cells actively suppress the antileukemic response in this system. Functional experiments such as add-back of isolated tolerogenic dendritic cells to Kit-M treated cultures or blocking antibodies against ILT-3 or CTLA-4 are necessary to support the mechanistic model.

The clinical correlative data presented in Figure 6 are also problematic. The authors compare tolerogenic dendritic cell frequencies between ELN risk groups and between responders and non-responders to induction chemotherapy, yet they explicitly state that none of these comparisons reached statistical significance. Despite this, they present the data in bar graphs within the main text as if to suggest meaningful trends. With only eighteen patients, these analyses are underpowered, and presenting non-significant findings in this manner is misleading. The cohort itself is heterogeneous, including both newly diagnosed patients and relapsed or post-transplant cases, whose T-cell repertoires and dendritic cell profiles are fundamentally different. A sensitivity analysis excluding the two non-primary cases should be performed to ensure the consistency of the Kit-M effects. At minimum, these clinical comparisons should be moved to supplementary materials with a clear acknowledgment of their exploratory nature.

A further concern relates to the use of PGE1 in the Kit-M cocktail. Prostaglandin E1 and E2 are widely cited in the literature as promoters of tolerogenic dendritic cells and myeloid-derived suppressor cells. The authors propose their combination with GM-CSF for maturation of leukemia-derived dendritic cells, yet they do not adequately explain why, at the specific concentration used, this combination favors an immunostimulatory rather than an immunosuppressive phenotype. A more rigorous discussion or citation of data addressing this paradox is required to align with mechanistic expectations.

Finally, the flow cytometry gating strategy is not adequately documented. The authors describe identifying leukemia-derived dendritic cells based on co-expression of blast markers such as CD117 and dendritic cell markers such as CD80, but they provide no gating strategy in the main text or supplementary materials. Without a clear illustration of how these rare dual-positive populations were discriminated from doublets and non-specific staining, the accuracy of the reported frequencies cannot be verified. This omission is particularly problematic given that the central claims depend on precise flow cytometric identification.

Minor Issues for Revision

The statistical methods require adjustment. The authors define a category of "borderline significance" for p-values between 0.10 and 0.05, which is non-standard and should be eliminated. All p-values should be reported exactly rather than as ranges, and the conventional threshold of 0.05 should be applied consistently. For non-normally distributed data or small subgroups, non-parametric tests such as the Wilcoxon signed-rank test would be more robust than the paired t-test.

Several typographical and formatting errors detract from clarity. Section 3.2.3.2 appears twice consecutively on page 9 due to a copy-paste error that must be corrected. The figures, particularly Figures 1 and 2, are difficult to read because the subpanel labels are not clearly visible and the text within the figures is too small. Figure 5 is especially problematic, as the panels referenced in the text are not clearly delineated, and the caption appears incomplete. Additionally, the authors use inconsistent nomenclature for tolerogenic dendritic cells, switching between "DCt" and "DCtol" throughout; a single consistent term should be adopted.

The discussion overreaches by extensively referencing previous in vivo studies to suggest that Kit-M works in patients. While contextualizing findings is appropriate, the discussion should focus primarily on the ex vivo data presented here. The repeated emphasis on in vivo effects gives the impression that those findings are demonstrated in this manuscript, which they are not. A more restrained discussion that clearly delineates what the present experiments demonstrate and what remains to be proven would strengthen the manuscript.

Regarding Figure 5, the presentation of "Cases with lysis" alongside the cytotoxicity data is somewhat redundant. Consolidating these panels would improve readability. The terminology should also be consistent: the use of "tendentially" on line 251 should be replaced with "a trend towards significance" for clarity.

The work is informative and the Kit-M strategy is promising. However, the manuscript requires substantial revision to address the specificity controls, mechanistic validation, statistical robustness, and methodological documentation outlined above. With these corrections, the study could provide a meaningful contribution to the field of dendritic cell-based immunotherapy in AML.

Author Response

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Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

The manuscript "Blast-/immune modulatory Kit-M (GM-CSF+PGE1) reduces frequencies of tolerogenic dendritic cells and increases antileukemic cytotoxicity", written by Hartz et al. describes the effects of the  treatment of acute myeloid leukemia cells with a combination of cytokines and prostaglandins which increased the percentage of dendritic cells with antileukemic activities.

Introduction gives all the necessary information about the topic. Materials and methods could be described with more details (not in supplementary material). Although some data can be in supplementary material, I think, abbreviations should not. It is hard to read the text with so many abbreviations which are not explained. They should also be explained below each figure. The description of the results requires small introduction, to repeat which samples were analyzed, what was done and how ("DCtol after DC/MLC"?). This stands for all the paragraphs. Data should be described with full sentences, not as notes in parentheses (i. e. "DCleu/WB:DC(M)"...) because it is very difficult to follow. Too many abbreviations can also be avoided. Frequencies can be put in table (not supplementary). In second paragraph of the Results it should be explained how tolerogenic DC subtypes were determined, which antibodies were used and why (some of these information are explained in the Discussion). Also other paragraphs should be written in the same way: explanation of the experiment and samples, and the results (paragraph 3.2, 3.3). All data should be presented (also for healthy samples). In the Results, obtained data are often compared with published data. This should be done in the Discussion. Improved lysis is not explained enough. Also in paragraph 3.4 it should be described how were samples analyzed, how were they divided (criteria in more details). Discussion is in general well written. Again, writing in the form of notes, in the parentheses can be avoided. Also, if some words are used only once, it is not necessary to write the abbreviation. It is not necessary to have separate paragraph for each result.

Comments:

line 36: "remission of the disease"?

line 114: sign % should be after the number. Supplementary material is not available.

line 130: although some information (such as antibody list or others) can be in the Supplementary material (which is also not available), abbreviations should be in the text (such as NK, CIK, DCleu, Kit-M)(DCM).

line 140, 153: abbreviations should not be in the title, but explained in the text below.

line 173: statistically, p is <0.05 or highly significant <0.005.ž

line 179: DCtol – explanation of abbreviation

line 182: explanations of abbreviations and parentheses should be avoided in the titles

line 188, 189: cells were generated, not frequencies, percentage should be written after number

all figures: explanation of all abbreviations, short explanation of the method and samples

line 239, 261: parentheses in the title should be avoided. If statistically something is borderline, it can be (only) discussed.

line 271: it is not IFNy, but IFN gamma (γ)

line 135: it is not clear what control group is;  what are "cases"

line 355: explanation of ELN risk groups (in methods)

line 356: what does it mean clear, although nonsignificantly lower frequencies?

line 400: sentence reorganization

 

Author Response

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Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

Hartz et al. investigated the DC modulation upon GM-CSF + PGE1 induction. 

1) Title: "Blast-/ immune modulatory Kit M" is not a standard term. suggest to remove it or modify it. Besides, there is no direct causal evidence on the cytotoxicity. Please use "associated" 

2) Introduction: Research gap not clear. What is the current practice in DC-based immunotherapy? Is DC important in the immunotherapy of leukemia? What are the limitations? What are the specific mechanisms that leukemic cells escape from immunotherapy, and how is GM-CSF + PGE1 now a focus (literature support)? Please include other groups' research findings. 

3) Sample size: Please show the sample size calculation. Is it now an underestimation? The sample size is too small. For example, you only have 1 subject for relapse after stem cell therapy. How to compare and analyse statistically?

4) Line 99: How does the author define the "acute phase of AML"?
Line 107: Secondary AML should not be included for analysis as its pathogenesis is different from primary AML, not to mention the different signatures across the subtypes. 

5) Experimental design: Note that all the experiments are performed ex vivo. We are not sure whether this can be replicated in animal or human models with complex tumour microenvironments and body immune response/regulation. Please put this as one limitation 

6) Ficoll separation. Please specify the Ficoll product and catalogue number

7) Despite the previous cited works, no confirmation/information on immunostaining for CD markers, no culture procedure is disclosed. Are the authors using the same reagents from the same manufacturers? For reproducibility of the study, please briefly state the procedure, reagents (catalogue number), instruments, etc. 

8) No supplementary data being uploaded. 

9) MLC: The authors isolated the T cells by tagging on CD3. CD3 is part of the TCR complex and binding will lead to activation and alter the baseline. How do the authors ensure the T cell response is not confounded by this procedure?

10) Analysis: It is not a typical way to show significance (**) with a p-value ≤0.005. Please justify it. Please provide literature support for the correlation coefficient.

11) Figure 1: showing the DC/WB is fine but for specific subtypes like DCleu or DCmat, the authors shall relative it to whole DC. As the DC number is higher upon induction, relative to WB does not indicate the percentage changes. Please do as like Figure 2.

12) Figure 1 & 2: These graphs are displayed in Mean+/- SD? There are many bars are overlapping and yet still showing significant differences. Similar goes with normal subjects (with overlapping pattern) but returned in no significant differences. 

13) Figure 1&2: Why were multiple runs of the paired T-test? This approach has resulted in a high risk of type 1 error. 

14) Figure 5: Kindly show us the SD or SEM

15) Figure 5 & 7: Is blast lysis occur within the peripheral blood of the patient? If it is not, why is it now having T cytotoxic and lysis of blast cells upon co-culture, where they are both isolated from the same origin? 

16) Please make sure to include the supplementary data for peer review 

17) Please review the writing and avoid overclaim or overstated conclusions. There is no direct evidence, and based on Fig 7, that's merely an association. 

18) What is the importance of this study, as compared with the previous works? From discussion, mostly the authors stated confirmation (repetition) from previous works. 

19) The current immunomodulation is due to GM-CSF or PGE1, or as both? Can this effect be stimulated via GM-CSF alone (or PGE1)? Any sufficient evidence to prove this? 

20) What is the direct implications or translational relevance from this study? 

21) Please include the date of ethical approval

Author Response

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Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

Thank you for your detailed point-by-point response and for the revisions made to the manuscript. I acknowledge that you have moderated some of the language, moved the underpowered clinical correlative data to the supplementary materials, added a gating strategy illustration, and included disclaimers regarding the correlational nature of your findings. These changes have improved the manuscript.

However, after a thorough re-evaluation, I must conclude that two major issues identified in my first review have not been adequately resolved. The revisions made to date are largely semantic or consist of disclaimers rather than substantive corrections to the experimental limitations or the narrative framing. Below, I explain why these issues remain and what is required to address them.

The first unresolved issue concerns the claim of antileukemic or leukemia-selective cytotoxicity. Your cytotoxicity assay uses only autologous blasts as target cells and includes no control targets such as autologous non-leukemic cells or allogeneic blasts. This design cannot distinguish between T-cell receptor-mediated recognition of leukemia-associated antigens and non-specific killing by innate effector cells such as natural killer cells. While you have added a disclaimer in the discussion, the abstract and the results sections continue to present the findings as “antileukemic” or even “leukemia-specific” activity without sufficient qualification. A disclaimer does not replace the need for appropriate experimental controls or, at a minimum, consistent language throughout the manuscript that reflects the absence of specificity data. The term “blast lysis” is factually accurate; “antileukemic cytotoxicity” implies a selectivity that has not been demonstrated. This remains a core interpretative flaw.

The second unresolved issue is the lack of functional evidence for a causal role of tolerogenic dendritic cells in the observed effects. You report negative correlations between the frequency of tolerogenic dendritic cells and blast lysis, and you interpret this as evidence that Kit-M enhances immunity by reducing these suppressive subsets. Correlation does not establish causation, and you have not performed any functional experiments to test this mechanism, such as add-back of isolated tolerogenic dendritic cells or blocking antibodies against ILT-3 or CTLA-4. While I accept that such experiments are technically challenging due to low cell yields, the narrative of the manuscript continues to present the reduction of tolerogenic dendritic cells as part of a mechanistic pathway rather than as an association that requires causal validation. The discussion still contains sentences that imply direct causality, such as “Kit-M reduces DCtol and leads to improved antileukemic activity.” This overreach must be corrected by clearly separating observed associations from hypothetical mechanisms.

For the manuscript to be acceptable for publication, you must undertake the following revisions without requiring new experiments. First, remove the term “leukemia-specific” entirely from the abstract and all other sections, and consistently replace “antileukemic cytotoxicity” with “cytotoxicity against autologous blasts” or simply “blast lysis,” with an explicit statement in the discussion that the selectivity of killing remains unknown. Second, restructure the discussion to separate observed associations from hypothetical mechanisms, moving any causal language regarding tolerogenic dendritic cells to a clearly labeled hypothesis section and revising the conclusion to state only what has been demonstrated: that Kit-M treatment is associated with both reduced tolerogenic dendritic cell frequencies and increased blast lysis in ex vivo cultures. Additionally, add a sentence in the statistical methods acknowledging that no correction for multiple comparisons was applied and that p-values should be interpreted as nominal significance.

The Kit-M strategy is promising, and the paired whole-blood design is a strength. However, the current manuscript overstates its findings relative to the experimental evidence. With the essential revisions outlined above, which require no new data but a more honest and precise framing of what the experiments actually demonstrate, I would be pleased to recommend acceptance. Without these changes, the manuscript cannot be published in its present form.

Author Response

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Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

The authors of the manuscript „Treatment of Leukemic Blood Samples with Granulocyte-Macrophage-Colony Stimulating-Factor Combined with Prostaglandin E1 is Associated with Reduced Frequencies of Tolerogenic Dendritic Cells and Increased Antileukemic Cytotoxicity“ responded to most of the comments. Figures are better described now and the authors corrected the sentences  mentioned in minor comments, and explained the abbreviations. However, explanations of the method (i. e. antibodies) used for detection of certain types of cells are still missing (i. e. Fig. 6). These data are also missing in the Results (i. e. 3.23.¸, page 372,). CTX fluorolysis assay is described, but is not named.

Minor comments

line 364: sentence reorganization

Fig. 3: how cell frequences were assesed

line 372: how were T_IFN and others assesed

Figure 4. and other figures: explanation of MLC

line 621: reference?

Author Response

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Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

3.: Sample size: Please show the sample size calculation. Is it now an underestimation? The sample
size is too small. For example, you only have 1 subject for relapse after stem cell therapy. How to
compare and analyse statistically?
We included all available blood samples of AML patients in ‘acute (blast containing) phases of
the disease (first diagnosis, relapse before or after SCT’, since preliminary data of our group have
shown, that DC/DCleu generation and induction of leukemia specific/antileukemic processes is
possible in leukemic PB (and BM samples) independent of SCT -, mutation-, HLA-status , gender
and age, secondary and primary disease etc (Unterfrauner et al., 2023, Klauer et al., 2025) and
even in MDS or lymphoid diseases (ALL,CLL), (Feng et al., 2025) despite of lower sample size we
could deduce significant data about the role of Kit M to downregulate suppressive DC and to reopen
the field for antileukemic processes. The relatively small sample size is justified by prior
evidence demonstrating that the anti-leukemic activity is independent of key patient
characteristics, including age, sex, ELN risk score, response to induction chemotherapy, disease
stage, and leukemic blast counts (Klauer et al., 2025).

Follow-up comment: The authors did not address my comment. Please provide the sample size calculation. If it was not performed, kindly justify the reason.

 

5.: Experimental design: Note that all the experiments are performed ex vivo. We are not sure
whether this can be replicated in animal or human models with complex tumour
microenvironments and body immune response/regulation. Please put this as one limitation

This is an important comment: we use a WHOLE BLOOD MODEL: heparinized patients’ samples
are included- containing all potentially activating or suppressive cellular or soluble components
of the patients – thereby simulating the in vivo situation in leukemically diseased organisms
(animals/patients) most. The experiments in this study were solely performed ex vivo. However,
recent studies from our work group have shown the immune modulating effects of Kit-M in vivo.
As cited in this study, Atzler et al. and Filippini Velázquez et al. have published data suggesting
that Kit-M (containing the clinically approved drugs GM-CSF and PGE1) is able to produce
DC/DCleu in vivo in both leukemia-diseased rats and humans – leading to changed (more
favorable) compositions of immune cells and a reduction or at least stabilization of heavily
diseased and pretreated AML patients before or after SCT (Atzler; Filippini)
Our in vivo findings are preliminary, as they are based on a limited number of (treated) animals
and human subjects. The ex vivo findings presented here underline the effects of Kit M in
modulating blasts to DCleu, reducing tolerogenic DCs-thereby re-establishing antileukemic
reactions and reducing tumor cells. We include some sentences in discussion.

Follow-up comment: Ex vivo findings are not always equivalent to patient outcomes, as there is no systemic ADME involvement. In addition, ex vivo models lack systemic organ interactions, including those involving the liver, lungs, and kidneys. Please address these limitations accordingly. 

 

13: Figure 1&2: Why were multiple runs of the paired T-test? This approach has resulted in a
high risk of type 1 error.
All comparisons between conditions were performed using two-tailed paired Student’s t-tests,
as the samples originate from the same patients and therefore represent dependent
observations. We acknowledge that multiple paired t-tests across different cell populations may
increase the risk of type I error. However, the analyses were conducted in an exploratory
framework aiming to identify biologically relevant differences between predefined immune cell
subsets. Therefore, no correction for multiple testing was applied. This limitation has now been
explicitly stated in the revised manuscript.

Follow-up comment: Disagree with this, and the authors should be careful when addressing this issue. As the authors are aware of the risk of Type I error, what appears to be biologically relevant may actually represent a false positive. It is a must to perform either repeated-measures ANOVA or multiple t-tests with corrected p-values upon an adjustment based on the number of repeated statistical comparisons.

 

17: Please review the writing and avoid overclaim or overstated conclusions. There is no direct
evidence, and based on Fig 7, that's merely an association.
Figure 7 gives correlation analyses including on the x axis delta values between KITM treated vs
untreated samples and correlating these findings with improved lysis- differences are highly
significant, demonstrating, that KitM pretreatment INCREASES DCleu and DECREASES
tolerogenic DC or T cells. We revise in part discussion.

Follow-up comment: The authors did not address my concern. Please do not overclaim the findings, as correlation does not imply causation or regression. A simple correlation analysis does not establish a causal relationship between variables.

 

Additional comments: 
A) Figure S4: Kindly show the flow dotplot graphs for isotype control as well.

B) Supplementary for Materials and Methods (Flow Cytometry): Please include the catalogue numbers for all the antibodies used, including isotype controls. 

C) Lines 124-144 (Patients' Characteristics): When were the patient samples collected? Please update the methodology section (for example, Line 125) to include the ex vivo collection timeframe (for example, 2018–2020). Kindly update Table S1 to include each patient’s initial diagnosis date, ex vivo sample collection date, and treatment history (if possible). This is important because ex vivo samples may behave differently due to the effects of recent chemotherapy.

Author Response

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Author Response File: Author Response.pdf

Round 3

Reviewer 3 Report

Comments and Suggestions for Authors

Issues Requiring Correction
1.SAMPLES USED
1.a. We did not do a ‘sample size’ calculation, but used all samples we could get from the hospitals from AML patients in blast rich phases of the disease (first dgn, relapse before and after SCT), since analyses of our group before showed, that the induction of blast lysis is independent of -e.g stages, HLA; sex, age, mutation and transplantation status (Klauer et al 2025).
Follow-up comment: This is now an issue, as some of the subgroups are very small in number. Without a sample size calculation, it is unclear whether a sufficient number of subjects has been collected for a valid analysis. Although uncommon, this can still be acceptable if the authors perform a sample size calculation now and justify that the recruited sample size is scientifically and statistically sufficient. 

3.STATISTICS in Fig 1 and 2: ANOVA vs paired T-test
3.1. Since the analysis involves only two groups (Kit M pretreated vs not pretreated Control group), performing a one-way ANOVA would be redundant, since, for two-group comparisons, ANOVA and the independent samples t-test yield identical results (F = t²). Therefore, the t-test was considered the most appropriate statistical approach and we keep the static.

Follow-up comment: The issue is not the number of groups, but rather the high risk of Type I errors. As pointed out in the earlier comments, there appears to be inconsistency in the reported statistical significance (treated vs untreated). A false-positive findings cannot be ruled out, and the authors should perform the analysis using an appropriate and statistically valid approach. At the very least, the authors should apply adjusted p-values for multiple t-test comparisons to reduce the risk of inflated Type I error rates.

5.Figure S4: dot plot for isotype
5.1: We include the isotype figure after culture with Kit M : on the left side you find
isotype controls, on the right side DC and blast markers. You see the increased SSC, typical for DC or DCleu.

Follow-up comment: Please provide the raw data for both the isotype control (%) and CD-labeled (%) populations to allow proper evaluation of the gating strategy and interpretation of the flow cytometry results. Based on the current response, it is unclear how the authors derived the isotype control measurements, whether they were obtained directly from experimental measurement or inferred solely through the gating strategy.

Author Response

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Author Response File: Author Response.pdf