CNDP1 and Diabetic Kidney Disease: From Genetic Susceptibility to Therapeutic Targeting

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript presents CNDP1 as one of the “more extensively characterized DKD susceptibility loci,” yet large contemporary GWAS of DKD are not clearly shown to robustly replicate the Mannheim (CTG)₅ association.

Has the alleged protection of (CTG) against the disease reached genome, wide significance in the multi, ancestry GWAS studies of today? If the answer is no, how do the authors compare the early candidate, gene studies with the recent large, scale genomic datasets?

 

In fact, the odds ratios (e. g. , OR ~2. 56 protective) reported by early studies are extremely high for complex disease loci, which makes the finding suspicious. Could this reflect winner’s curse or population stratification? Has effect size attenuation been formally evaluated in meta-analyses?

 

The review acknowledges heterogeneity and failed replications but does not quantify them. What proportion of studies have replicated the association? Should we include a summary in the style of a forest plot or a structured meta, analytic synthesis?

The CTG repeat is a microsatellite and not a SNP. How reliably is this repeat detected or imputed in large biobank datasets? May technical genotyping limitations lead to bias in association estimates?

The paper almost exclusively focuses on genotype causing DKD protection. Is there any human Mendelian randomization data showing that genetically determined carnosinase activity is directly related to DKD outcomes? What are the effect sizes and confidence intervals if this is the case?

The animal knockout and overexpression models demonstrate biological plausibility. However, are there differences between murine and human carnosine metabolism that limit translational inference? Given species differences in serum carnosinase activity, how physiologically comparable are these models?

The manuscript interprets diabetic redistribution of CNDP1 expression (pages 6–7) as mechanistically deleterious. What was the size of the sample for human kidney tissue studies that backed this up? Was this discovery reproduced in other independent groups?

One can see the paradox of lower mRNA but higher protein in diabetic kidneys. Is there quantiative proteomics data showing increased CNDP1 protein levels or is it only based on the semi, quantitative immunohistochemistry? Could variations in antibody specificity or glycosylation mislead the interpretation?

The eQTL section concludes that the CTG repeat acts post-translationally. Has this been directly demonstrated in human tissue? Could there be unrecognized regulatory variants in LD contributing to disease association?

The manuscript suggests serum carnosinase may outperform genotype in risk prediction. Has incremental predictive value (ΔC-statistic, NRI, IDI) been demonstrated over established DKD risk models? Are associations independent of eGFR, albuminuria stage, and inflammation?

Since serum carnosinase levels are lower in later stages of CKD, how reliable and unaffected by the stage is this biomarker? Does serum carnosinase activity have any intra, individual variability data?

The most powerful RCT mentioned (pediatric T1DM, n=90, 12 weeks) is a short, term study. Is there evidence that albuminuria reductions were maintained after treatment stopped? Was there adjustment for regression to the mean?

The magnitude of UACR reduction (58%) appears unusually large for adjunct therapy. Was this trial independently replicated? Were patients on optimized renin, angiotensin, aldosterone system (RAAS) blockade and sodium, glucose cotransporter, 2 (SGLT2) inhibitors?

The meta-analysis cited involves different populations (prediabetes, T2DM). Were renal, specific endpoints considered, or only glycemic parameters?

No renal long, term hard endpoints (eGFR slope, ESRD) are reported. Is it too early to designate carnosine as renoprotective?

Carnostatine has potent preclinical activity. Have phase I trials in humans been started? What are the pharmacokinetic and safety issues? As carnosine has several systemic effects, what are the risks of long, term carnosinase inhibition (e. g. , neurological or oncologic effects)?

Since the brain shows the highest level of CNDP1 expression (Figure 1, page 5), what effects on the brain might systemic inhibition have?

The article mentions genotype, directed therapy. What is the absolute risk change due to the CTG genotype? Is the number needed to genotype (NNG) a good economic decision?

Given that (CTG) homozygosity is a rare occurrence among African and East Asian populations, does this imply a risk that the proposed healthcare strategy could exacerbate health inequalities?

Is there any evidence suggesting that the genotype can be a predictor of the response to carnosine supplementation or the use of carnosinase inhibitors?

The paper refers to CNDP1 as a translational genomics paradigm. How does its set of evidence stand relative to that of APOL1, UMOD, or SGLT2 pathway genetics in kidney disease? Are the authors giving a fair weight to human clinical evidence in making their conclusion?

The story is telling a neat genotype mechanism therapy line. Could this be an over, simplification of the multi, gene and multi, factorial nature of diabetic kidney disease?

The article needs a methods section detailing: How the literature was searched, What were the inclusion/exclusion criteria, Is the article a systematic or a narrative review, Also, there is no description of risk, of, bias assessment for the clinical trials cited.

Figures seem to be more conceptual than data, driven (e. g. , Figure 3, page 8). Are quantitative effect sizes represented accurately?

The review does not properly set apart: Type 1 vs Type 2 diabetes, Early vs advanced DKD, Albuminuric vs non, albuminuric DKD

Heritability is given as 29% (SE 0. 20). Is that SE correct (very large relative to estimate)? What is the confidence interval?

Allele frequencies are presented without source attribution in Table 1. Are these pooled estimates? What is the sample size per population?

The manuscript does not quantify: Population attributable risk, Absolute risk reduction, Effect size compared to current standard therapies

Given the therapeutic emphasis, do any authors have intellectual property related to carnosinase inhibition?

Since ChatGPT was used to generate figures (page 12), were those figures validated for scientific accuracy?

Author Response

We are deeply grateful to Reviewer 1 for the exceptionally thorough and rigorous evaluation of our manuscript. The reviewer’s detailed and insightful questions have identified important areas where our original presentation lacked the nuance and critical balance that this topic demands. Each comment has prompted substantive revisions that have, in our view, substantially strengthened the scientific rigor and transparency of this review. Below, we provide point-by-point responses to each comment. All manuscript revisions are indicated in red text in the revised manuscript.

Comment 1:

The manuscript presents CNDP1 as one of the “more extensively characterized DKD susceptibility loci,” yet large contemporary GWAS of DKD are not clearly shown to robustly replicate the Mannheim (CTG)₅ association. Has the alleged protection of (CTG) against the disease reached genome-wide significance in the multi-ancestry GWAS studies of today? If the answer is no, how do the authors compare the early candidate-gene studies with the recent large-scale genomic datasets?

Response 1:

We sincerely appreciate the reviewer raising this fundamental question, which strikes at the core of how CNDP1 evidence should be interpreted in the current genomic landscape. The reviewer is entirely correct: the Mannheim (CTG)₅ association has not reached genome-wide significance (p < 5 × 10⁻⁸) in any contemporary multi-ancestry GWAS of DKD. This is an important limitation that was insufficiently addressed in our original manuscript.

We have added inline caveats in Section 3.2 that explicitly state this and provides the technical explanation: the CTG repeat is a microsatellite polymorphism not captured on standard GWAS genotyping arrays (e.g., Illumina Global Screening Array) and is poorly imputed from flanking SNPs due to the inherent difficulty of imputing short tandem repeats from surrounding linkage disequilibrium structure. Multi-ancestry GWAS further dilute population-specific signals by pooling populations with dramatically different allele frequencies. The original CNDP1 findings derive from smaller, hypothesis-driven candidate-gene studies, and we now frame them accordingly—emphasizing that CNDP1’s strength lies in functional validation and mechanistic coherence rather than GWAS-level statistical significance. (Revised manuscript, Section 3.2, inline after OR 2.56 discussion)

Comment 2:

In fact, the odds ratios (e.g., OR ~2.56 protective) reported by early studies are extremely high for complex disease loci, which makes the finding suspicious. Could this reflect winner’s curse or population stratification? Has effect size attenuation been formally evaluated in meta-analyses?

Response 2:

We completely agree with the reviewer’s skepticism. An OR of 2.56 is indeed unusually large for a complex disease locus—typical GWAS-validated loci for complex traits report ORs in the 1.1–1.5 range—and this magnitude warrants careful scrutiny.

In the revised manuscript, we have added explicit discussion in the inline caveats in Section 3.2 flagging the OR of 2.56 as notably large for a complex disease locus and likely reflecting winner’s curse—the well-documented tendency for initial discovery studies to overestimate effect sizes due to stochastic variation in small samples. The primary association analysis was performed on a modest sample (n = 242: 135 cases with diabetic nephropathy and 107 controls without nephropathy), which increases vulnerability to both winner’s curse and residual population stratification in the case-control design. We further note that subsequent replication studies have generally reported attenuated effect sizes, consistent with regression to the mean. To our knowledge, formal evaluation of effect size attenuation via funnel plot asymmetry or Egger regression has not been systematically performed in published meta-analyses of CNDP1, and we identify this as a gap. (Revised manuscript, Section 3.2 inline caveats)

Comment 3:

The review acknowledges heterogeneity and failed replications but does not quantify them. What proportion of studies have replicated the association? Should we include a summary in the style of a forest plot or a structured meta-analytic synthesis?

Response 3:

We thank the reviewer for this important suggestion. The original manuscript’s treatment of replication heterogeneity was indeed insufficient. In the revised manuscript, we have added a quantitative summary in the methodological context paragraph: among approximately 10 independent association studies examining the (CTG)₅ variant and DKD, roughly half have reported statistically significant protective associations (predominantly in European and Arab cohorts), while the remainder have failed to replicate—notably in African American, Pima Indian, and some East Asian populations. Sources of heterogeneity include population-specific allele frequencies, varying sample sizes, differences in phenotype definition (albuminuria versus ESRD versus eGFR decline), and diabetes type (T1DM versus T2DM).

Regarding the suggestion of a forest plot or formal meta-analytic synthesis: we agree that such an analysis would be highly informative and represent a valuable contribution to the field. However, as this manuscript is a narrative review (now explicitly stated at the end of the Introduction), conducting a formal meta-analysis falls outside its scope. We have acknowledged this as a worthwhile future direction. (Revised manuscript, Section 3.2 inline caveats)

Comment 4:

The CTG repeat is a microsatellite and not a SNP. How reliably is this repeat detected or imputed in large biobank datasets? May technical genotyping limitations lead to bias in association estimates?

Response 4:

This is an excellent and technically important point that we had failed to address adequately. The CTG repeat requires fragment analysis or capillary electrophoresis for accurate length determination and is not genotyped on standard GWAS arrays. Microsatellite sizing is additionally subject to stutter artifacts and inter-laboratory variability, which can introduce measurement error. The repeat cannot be reliably imputed from flanking SNPs in large biobank datasets (UK Biobank, All of Us), which likely explains its absence from GWAS catalogs despite the strong prior linkage evidence at 18q22.3.

These technical constraints mean that the absence of CNDP1 from modern GWAS results does not necessarily indicate a lack of genuine association—it may instead reflect an inability to test the relevant variant. We discuss this in the inline caveats in Section 3.2 and note that emerging long-read sequencing technologies may enable more reliable microsatellite detection in future biobank studies. (Revised manuscript, Section 3.2 inline caveats)

Comment 5:

The paper almost exclusively focuses on genotype causing DKD protection. Is there any human Mendelian randomization data showing that genetically determined carnosinase activity is directly related to DKD outcomes? What are the effect sizes and confidence intervals if this is the case?

Response 5:

We thank the reviewer for highlighting this important gap in causal inference. Huang et al. (2024) [reference 49 in our manuscript] performed Mendelian randomization analyses examining causal relationships between carnosine metabolism genes and diabetic nephropathy outcomes, providing preliminary MR support for a causal direction. However, we acknowledge that the specific effect sizes for CNDP1-instrumented carnosinase activity on DKD endpoints were modest, and the instruments are limited by the difficulty of identifying strong genetic proxies for carnosinase activity specifically (given that the CTG repeat itself is not in standard GWAS panels used for instrument selection).

We have added a sentence at the end of Section 3.5 referencing this MR evidence and noting that formal two-sample MR using carnosinase activity as the exposure and hard DKD endpoints as the outcome remains an important evidence gap to be addressed in future studies with appropriate instruments. (Revised manuscript, Section 3.5, end of paragraph)

Comment 6:

The animal knockout and overexpression models demonstrate biological plausibility. However, are there differences between murine and human carnosine metabolism that limit translational inference? Given species differences in serum carnosinase activity, how physiologically comparable are these models?

Response 6:

We are grateful for this critical translational question, which addresses a fundamental limitation we had not adequately discussed. The reviewer is correct that there are significant species differences. Mice lack the signal peptide in the CNDP1 gene and consequently do not express serum carnosinase-1 (CN-1) in circulation at levels comparable to humans. In fact, wild-type rodents have very low or absent circulating carnosinase activity, resulting in inherently higher baseline carnosine concentrations. This means that Cndp1-knockout mice represent a model of further elevating already-high tissue carnosine rather than directly recapitulating the human (CTG)₅ phenotype, where reduced but still present carnosinase activity leads to modestly higher carnosine levels.

Transgenic mice overexpressing human CNDP1 partially address this limitation by introducing human-like serum carnosinase activity into a murine background. We have added 1–2 sentences in Section 5.3 explicitly discussing these species differences and their implications for translational inference, noting that while the animal models establish biological plausibility, direct extrapolation to human DKD should be made cautiously. (Revised manuscript, Section 5.3, inline addition)

Comment 7:

The manuscript interprets diabetic redistribution of CNDP1 expression (pages 6–7) as mechanistically deleterious. What was the size of the sample for human kidney tissue studies that backed this up? Was this discovery reproduced in other independent groups?

Response 7:

We appreciate the reviewer’s attention to the evidentiary basis for these claims. The kidney expression data from Janssen et al. [4] derived from a small number of specimens—approximately n = 10 per group—obtained from nephrectomies. The Peters et al. [18] study similarly used a limited number of human kidney samples for quantitative protein analysis. To our knowledge, neither the diabetic redistribution finding nor the mRNA–protein discordance has been independently replicated in larger tissue biobank cohorts.

We have added explicit language in Section 4.3 specifying these sample sizes and acknowledging the absence of independent replication, making clear that these findings should be considered preliminary until validated in larger studies. (Revised manuscript, Section 4.3, end of paragraph)

Comment 8:

One can see the paradox of lower mRNA but higher protein in diabetic kidneys. Is there quantitative proteomics data showing increased CNDP1 protein levels or is it only based on the semi-quantitative immunohistochemistry? Could variations in antibody specificity or glycosylation mislead the interpretation?

Response 8:

The reviewer correctly identifies a significant methodological concern. The protein-level evidence relies entirely on semi-quantitative immunohistochemistry (IHC), which cannot provide absolute quantification and is inherently susceptible to variability in antibody specificity, tissue fixation, and staining protocols. To our knowledge, no unbiased quantitative proteomics study (e.g., mass spectrometry-based targeted or shotgun proteomics) has specifically quantified CNDP1 protein abundance in diabetic versus non-diabetic human kidneys.

Furthermore, as the reviewer astutely notes, glycosylation differences in the diabetic milieu could alter antibody epitope accessibility and confound IHC interpretation. CNDP1/CN-1 contains three N-glycosylation sites, and hyperglycemia-associated changes in glycan processing could affect antibody binding independent of actual protein abundance changes. We have added these caveats in Section 4.3, along with a brief note that the discordance may reflect altered protein stability or clearance in the diabetic milieu, though this hypothesis requires validation through quantitative proteomic approaches. (Revised manuscript, Section 4.3, end of paragraph)

Comment 9:

The eQTL section concludes that the CTG repeat acts post-translationally. Has this been directly demonstrated in human tissue? Could there be unrecognized regulatory variants in LD contributing to disease association?

Response 9:

We thank the reviewer for this nuanced point. The proposed post-translational mechanism (reduced signal peptide hydrophobicity impairing ER targeting and glycosylation) has been demonstrated through in vitro cell-based studies but has not been directly confirmed in human kidney tissue in vivo. We acknowledge this distinction in the revised manuscript.

Regarding the possibility of unrecognized regulatory variants in LD: this is a legitimate concern. Haplotype analyses (discussed in Section 3.5) have identified SNPs such as rs2346061 and rs12957330 that show associations independent of the CTG repeat and the D18S880 microsatellite, suggesting that the CNDP1 locus harbors multiple functional variants. Some of these could operate through transcriptional regulatory mechanisms not yet characterized. We have added a caveat sentence at the end of Section 4.4 addressing both points. (Revised manuscript, Section 4.4, end of paragraph)

Comment 10:

The manuscript suggests serum carnosinase may outperform genotype in risk prediction. Has incremental predictive value (ΔC-statistic, NRI, IDI) been demonstrated over established DKD risk models? Are associations independent of eGFR, albuminuria stage, and inflammation?

Response 10:

The reviewer raises an essential point about clinical biomarker validation. No study has formally demonstrated incremental predictive value of serum carnosinase—via ΔC-statistic, net reclassification improvement (NRI), or integrated discrimination improvement (IDI)—over established DKD risk models incorporating eGFR, albuminuria, HbA1c, blood pressure, and inflammatory markers. The existing studies by Qiu et al. (2022) and Zhou et al. (2021) demonstrate associations between carnosinase levels and renal outcomes, but do not report formal reclassification or discrimination analyses against established clinical models.

We believe the existing language in Sections 6.1–6.2 adequately conveys that serum carnosinase is a candidate rather than validated biomarker, but we acknowledge the reviewer’s point that the language should not imply clinical readiness. We confirm that the independence of carnosinase associations from eGFR, albuminuria stage, and inflammation has not been rigorously established in multivariable models.

Comment 11:

Since serum carnosinase levels are lower in later stages of CKD, how reliable and unaffected by the stage is this biomarker? Does serum carnosinase activity have any intra-individual variability data?

Response 11:

We appreciate this important concern about biomarker reliability. The inverse relationship between serum carnosinase and advancing CKD stage introduces the possibility of reverse causation—declining carnosinase may be a consequence rather than a cause of progressive kidney dysfunction. This is discussed in Section 6.2, which notes that serum carnosinase may paradoxically decline as eGFR falls. To our knowledge, systematic intra-individual variability data (e.g., coefficient of variation across repeated measurements within the same individual over time) have not been published for serum carnosinase. Standardized assays with established reference ranges are also lacking. These are important gaps that should be addressed in future biomarker validation studies.

Comment 12:

The most powerful RCT mentioned (pediatric T1DM, n=90, 12 weeks) is a short-term study. Is there evidence that albuminuria reductions were maintained after treatment stopped? Was there adjustment for regression to the mean?

Response 12:

The reviewer’s concerns are entirely valid. The Elbarbary et al. (2018) trial did not include a post-treatment follow-up period, so it is unknown whether the observed albuminuria reductions were maintained after cessation of carnosine supplementation. The study also did not explicitly adjust for regression to the mean, which is a legitimate statistical concern given that participants were selected for established albuminuria—a criterion that inherently enriches for individuals whose values may have been transiently elevated and could regress toward the mean independent of any treatment effect.

We have added 2–3 sentences in Section 7.1 after the trial results explicitly noting these limitations, emphasizing the need for longer-duration trials with extended post-treatment follow-up to distinguish genuine therapeutic effects from regression artifacts. (Revised manuscript, Section 7.1, inline addition after trial results)

Comment 13:

The magnitude of UACR reduction (58%) appears unusually large for adjunct therapy. Was this trial independently replicated? Were patients on optimized renin-angiotensin-aldosterone system (RAAS) blockade and sodium-glucose cotransporter-2 (SGLT2) inhibitors?

Response 13:

We agree that a 58% UACR reduction is unusually large for an adjunctive intervention. For context, landmark trials of SGLT2 inhibitors—now considered standard of care—typically report UACR reductions of 30–40%. This discrepancy should raise appropriate caution about the Elbarbary result.

The trial has not been independently replicated to date. Regarding background nephroprotective therapy: the study enrolled pediatric patients (ages 10–18) with type 1 diabetes in 2018. SGLT2 inhibitor use was not reported and was not standard of care in pediatric T1DM at that time. RAAS blockade use was also not clearly documented. The absence of optimized background therapy may inflate the apparent treatment effect, as participants may have had more modifiable albuminuria than would be seen in contemporary trials with RAAS blockade and SGLT2 inhibitors as standard of care. These caveats are addressed in the same Section 7.1 inline addition. (Revised manuscript, Section 7.1, inline addition)

Comment 14:

The meta-analysis cited involves different populations (prediabetes, T2DM). Were renal-specific endpoints considered, or only glycemic parameters?

Response 14:

We appreciate the reviewer drawing attention to this important distinction. The Li et al. (2025) meta-analysis aggregated eight randomized controlled trials across heterogeneous populations (prediabetes and T2DM) and assessed glycemic parameters only (fasting blood glucose, HbA1c). No pooled analysis of kidney function outcomes (e.g., UACR, eGFR change, time to ESRD) was performed, significantly limiting the meta-analysis’s direct applicability to DKD. We have added one sentence clarifying this distinction after the meta-analysis discussion in Section 7.1. (Revised manuscript, Section 7.1, inline addition after Li et al. discussion)

Comment 15:

No renal long-term hard endpoints (eGFR slope, ESRD) are reported. Is it too early to designate carnosine as renoprotective?

Response 15:

The reviewer is correct, and we fully concur with this assessment. No clinical trial of carnosine supplementation or carnosinase inhibition has demonstrated effects on hard renal endpoints—defined as sustained eGFR decline ≥40%, doubling of serum creatinine, progression to ESRD, or renal death. All available evidence pertains to surrogate markers (albuminuria, oxidative stress biomarkers) of uncertain durability. We have added explicit language in the Section 7.1 trial caveats stating that the current evidence base is insufficient to designate carnosine as definitively renoprotective, and that confirmation through adequately powered trials with hard renal endpoints remains essential. (Revised manuscript, Section 7.1, inline addition)

Comment 16:

Carnostatine has potent preclinical activity. Have phase I trials in humans been started? What are the pharmacokinetic and safety issues? As carnosine has several systemic effects, what are the risks of long-term carnosinase inhibition (e.g., neurological or oncologic effects)?

Response 16:

We thank the reviewer for raising these critical translational questions. To our knowledge, carnostatine (SAN9812) has not entered phase I clinical trials in humans as of early 2026. Several critical pharmacokinetic and safety questions remain unresolved, including oral bioavailability, plasma half-life, tissue distribution, potential drug-drug interactions, and the feasibility of achieving sustained CN-1 inhibition at therapeutically relevant levels.

Regarding safety: systemic carnosinase inhibition would elevate carnosine levels not only in kidney but across all tissues. Given that CNDP1 shows the highest expression in brain (Figure 1), neurological effects of sustained inhibition—whether beneficial (enhanced neuroprotection) or adverse (altered neurotransmitter metabolism)—require careful preclinical evaluation. The emerging pan-cancer associations of CNDP1 (Section 8.1), including its identification as a metabolic vulnerability in brain metastasis (Gomez-Munoz et al. 2025), raise additional theoretical oncologic safety questions. We have added 1–2 sentences at the end of Section 7.2 addressing the absence of human trials and the need for comprehensive preclinical safety evaluation. (Revised manuscript, Section 7.2, end of paragraph)

Comment 17:

Since the brain shows the highest level of CNDP1 expression (Figure 1, page 5), what effects on the brain might systemic inhibition have?

Response 17:

This important concern is addressed together with Comment 16 above. The brain-specific consequences of systemic carnosinase inhibition represent a critical knowledge gap. Carnosine participates in neurotransmitter modulation, pH buffering, and protection against oxidative and carbonyl stress in neural tissue. Whether pharmacological elevation of brain carnosine through peripheral CN-1 inhibition would produce net beneficial or adverse neurological effects is currently unknown and must be rigorously evaluated in preclinical safety pharmacology studies (including behavioral, cognitive, and neurotoxicity assessments) before human trials can be justified. (Revised manuscript, Section 7.2, same addition)

Comment 18:

The article mentions genotype-directed therapy. What is the absolute risk change due to the CTG genotype? Is the number needed to genotype (NNG) a good economic decision?

Response 18:

We appreciate the reviewer emphasizing the need for quantitative health economic assessment. The absolute risk reduction attributable to the CTG genotype has not been formally quantified. Given that approximately 30–40% of diabetic patients develop DKD and the protective OR for (CTG)₅ homozygosity is estimated at 2–2.5 (likely inflated by winner’s curse, as discussed in our response to Comment 2), the absolute risk reduction is likely modest. Cost-effectiveness analyses including NNG calculations have not been performed and would require assumptions about genotyping cost, intervention availability, and genotype-specific treatment benefit—none of which are currently established.

We have added a sentence in Section 7.3 explicitly identifying NNG and cost-effectiveness analysis as unresolved implementation questions. (Revised manuscript, Section 7.3, end of paragraph)

Comment 19:

Given that (CTG)₅ homozygosity is a rare occurrence among African and East Asian populations, does this imply a risk that the proposed healthcare strategy could exacerbate health inequalities?

Response 19:

This is a critically important ethical consideration that we had not adequately addressed. The reviewer is correct: a precision medicine strategy based on (CTG)₅ genotyping would disproportionately benefit European populations (where approximately 10–15% are protective homozygotes) while offering minimal clinical utility for African (<1% homozygous) and East Asian (<0.1% homozygous) populations—populations that already bear a disproportionate burden of DKD worldwide. Implementing such a strategy without simultaneously identifying alternative risk-modifying variants for non-European populations would risk exacerbating existing health disparities.

We have addressed this concern in the expanded Limitations section, where we explicitly warn about this equity dimension and emphasize the need for expanded genetic studies in underrepresented populations to identify population-specific risk variants. (Revised manuscript, Limitations section, new paragraph)

Comment 20:

Is there any evidence suggesting that the genotype can be a predictor of the response to carnosine supplementation or the use of carnosinase inhibitors?

Response 20:

To our knowledge, no clinical trial has stratified outcomes by CNDP1 genotype, so there is currently no direct evidence that genotype predicts differential response to carnosine supplementation or carnosinase inhibition. This is a critical evidence gap: demonstrating genotype-treatment interaction is a prerequisite for pharmacogenomically guided therapy. Mechanistically, individuals with longer CTG repeats (higher carnosinase activity) would be expected to derive greater benefit from carnosinase inhibitors, but this remains entirely hypothetical until tested in genotype-stratified clinical trials.

We have added this point in Section 7.3. (Revised manuscript, Section 7.3, end of paragraph)

Comment 21:

The paper refers to CNDP1 as a translational genomics paradigm. How does its set of evidence stand relative to that of APOL1, UMOD, or SGLT2 pathway genetics in kidney disease? Are the authors giving a fair weight to human clinical evidence in making their conclusion?

Response 21:

We sincerely appreciate this important critique, which we believe has led to the single most significant improvement in the revised manuscript. The reviewer is correct that our original framing overrepresented the maturity of CNDP1 evidence relative to more established kidney disease loci.

We have added a detailed comparison in the expanded Limitations section: APOL1 has achieved robust genome-wide significance across multiple studies, has clear Mendelian randomization support, a defined pathogenic mechanism (ion channel toxicity), and targeted clinical trials now underway (e.g., inaxaplin). UMOD is validated across multiple large GWAS with functional confirmation. The SGLT2 pathway provides the most advanced translational comparator, with SGLT2 inhibitors demonstrating hard renal endpoint benefits in large-scale RCTs (CREDENCE, DAPA-CKD, EMPA-KIDNEY). By these benchmarks, CNDP1 is at an earlier translational stage: genetic associations derive from candidate-gene studies without GWAS-level significance, replication is inconsistent, no hard endpoint trial data exist, and carnosinase inhibitors remain preclinical.

We have accordingly tempered the framing throughout the manuscript, and we believe the revised text now provides a more balanced and honest assessment. (Revised manuscript, Limitations section, new paragraph)

Comment 22:

The story is telling a neat genotype→mechanism→therapy line. Could this be an over-simplification of the multi-gene and multi-factorial nature of diabetic kidney disease?

Response 22:

We fully acknowledge this concern. DKD is a polygenic, multifactorial disease influenced by dozens of susceptibility loci, epigenetic modifications, gene-environment interactions, and modifiable risk factors. The genotype–mechanism–therapy narrative for CNDP1, while conceptually useful as an organizing framework, is necessarily a simplification. CNDP1 represents one component of a complex genetic architecture, and its individual contribution to overall DKD risk is modest relative to the aggregate effect of all genetic and environmental determinants.

We have added this acknowledgment in the expanded Limitations section. (Revised manuscript, Limitations section, same paragraph)

Comment 23:

The article needs a methods section detailing: How the literature was searched, What were the inclusion/exclusion criteria, Is the article a systematic or a narrative review, Also, there is no description of risk-of-bias assessment for the clinical trials cited.

Response 23:

We thank the reviewer for this recommendation. We have added search methodology language at the end of the Introduction, which explicitly identifies the article as a narrative review (not a systematic review or meta-analysis), describes the databases searched (PubMed/MEDLINE, Embase, Google Scholar), the search terms used (“CNDP1,” “carnosinase,” “Mannheim variant,” “diabetic kidney disease,” and related terms), the time frame (inception through January 2026), and the language restriction (English). We acknowledge that no formal inclusion/exclusion criteria and no risk-of-bias assessment were applied, consistent with narrative review methodology. Individual trial limitations are critically appraised throughout Section 7. (Revised manuscript, end of Introduction)

Comment 24:

Figures seem to be more conceptual than data-driven (e.g., Figure 3, page 8). Are quantitative effect sizes represented accurately?

Response 24:

We appreciate this observation. Figures 1 and 2 were generated using AI assistance but were subsequently validated by the authors against primary source databases (GTEx v8 for Figure 1 and the Kidney Interactive Transcriptomics database for Figure 2). Figure 3 is explicitly a conceptual schematic illustrating mechanistic pathways rather than a quantitative data representation—it does not depict specific effect sizes.

We have added a clarifying note in the Acknowledgements section specifying which figures are data-informed versus conceptual and describing the validation process. (Revised manuscript, Acknowledgements section)

Comment 25:

The review does not properly set apart: Type 1 vs Type 2 diabetes, Early vs advanced DKD, Albuminuric vs non-albuminuric DKD.

Response 25:

We agree that these are important pathophysiological distinctions. The CNDP1 literature spans both T1DM and T2DM populations with varying phenotype definitions, and we had not been sufficiently explicit about which diabetes type and DKD stage each study addressed. In the revised manuscript, we address this through the inline caveats in Section 3.2 and the expanded Limitations section, which acknowledge that this review does not systematically distinguish between these subgroups and that readers should consider these distinctions when interpreting individual studies. The expanded Limitations section further reiterates that these represent pathophysiologically distinct entities and that CNDP1 relevance may vary across them. (Revised manuscript, Section 3.2 and Limitations section)

Comment 26:

Heritability is given as 29% (SE 0.20). Is that SE correct (very large relative to estimate)? What is the confidence interval?

Response 26:

We thank the reviewer for flagging this. We have verified the value against the source publication (Kim et al., Diabetes 2022; 71:1137–1148). The SE of 0.20 is indeed correct as reported in the paper. This estimate derives from GREML-LDMS analysis on imputed SNP data from the UK Biobank NHW-Diabetes cohort. The approximate 95% CI is −0.10 to 0.69, which includes zero and reflects the considerable imprecision inherent in SNP-based heritability estimation for binary disease traits in moderately sized cohorts. We have added the 95% CI inline in Section 2.2 along with a sentence acknowledging this imprecision. (Revised manuscript, Section 2.2, inline addition)

Comment 27:

Allele frequencies are presented without source attribution in Table 1. Are these pooled estimates? What is the sample size per population?

Response 27:

We appreciate this attention to data provenance. The allele frequencies in Table 1 derive from individual studies, not pooled estimates. We have added a “Note on Table 1” paragraph immediately after the table providing specific source attribution and approximate sample sizes for each population: European (Janssen et al. [4], n ≈ 505; Freedman et al. [5], n ≈ 200); Arab (Janssen et al. [4], n = 192); African American (Freedman et al. [5]); East Asian (Kurashige et al. [13], n ≈ 3,400); American Indian (Chakkera et al. [10], n ≈ 350). (Revised manuscript, Note on Table 1, before Section 3.4)

Comment 28:

The manuscript does not quantify: Population attributable risk, Absolute risk reduction, Effect size compared to current standard therapies.

Response 28:

We acknowledge these omissions. Reliable calculation of population attributable risk and absolute risk reduction is precluded by the likely inflated ORs from early studies and the absence of hard endpoint trial data. Effect size comparisons with current standard therapies (SGLT2 inhibitors, GLP-1 receptor agonists, finerenone) are not possible given the fundamentally different evidence bases—CNDP1 has only surrogate endpoint data from a single small trial, whereas these comparator agents have large-scale hard endpoint RCT data. We have explicitly identified these as critical evidence gaps in the expanded Limitations section. (Revised manuscript, Limitations section, new paragraph)

Comment 29:

Given the therapeutic emphasis, do any authors have intellectual property related to carnosinase inhibition?

Response 29:

We confirm that none of the authors hold intellectual property, patents, licensing agreements, or financial interests related to carnosinase inhibitors, carnosine supplements, CNDP1 genotyping technologies, or any related therapeutic products. None of the authors have consulting relationships with companies developing carnosine-based therapies. The existing Conflicts of Interest statement (“The authors declare no conflicts of interest”) accurately reflects this position.

Comment 30:

Since ChatGPT was used to generate figures (page 12), were those figures validated for scientific accuracy?

Response 30:

Yes. All AI-generated figures were validated by the authors against primary source databases: Figure 1 was cross-referenced with GTEx v8 median TPM values; Figure 2 was verified against the Kidney Interactive Transcriptomics database (Humphreys Lab). Numerical values and relative expression patterns were independently confirmed. Figure 3 is a conceptual schematic illustrating mechanistic relationships and was reviewed for biological accuracy by all authors. We have expanded the Acknowledgements section to describe this validation process explicitly. (Revised manuscript, Acknowledgements section)

Reviewer 2 Report

Comments and Suggestions for Authors

This manuscript provides a thorough and updated synthesis of the CNDP1-DKD relationship that would be valuable to the nephrology and genetics communities.

Suggestions:

- In Section 4.3, the authors note the paradox of reduced mRNA but elevated protein in diabetic kidneys. Providing a brief hypothesis on the mechanism of altered post-translational regulation in the "diabetic milieu" would show a deeper level of critical thinking. For instance, could hyperglycemia affect the glycosylation or protein stability of CN-1 independently of its genetic signal peptide efficiency?

- In Section 5.1, the description of carnosine acting as a "sacrificial substrate" is excellent. To improve this further, you might briefly mention if there are any known "off-target" effects of carnosine-carbonyl adducts before they are excreted, or confirm they are biologically inert

- Consider adding a "Figure 4" that summarizes the clinical pipeline—from genetic screening to therapeutic intervention—to provide a forward-looking conclusion to the "Precision Medicine" section

- The Recent Advances" section (Section 8) mentions CNDP1 in cancer and heart failure. To prevent this section from feeling like a list of unrelated facts, add a sentence or two synthesizing why CNDP1 is relevant across these diverse pathologies. For example, explain if the common thread is the systemic regulation of carnosine's antioxidant properties or if it is a tissue-specific metabolic vulnerability

Author Response

We are sincerely grateful to Reviewer 2 for the thoughtful and constructive evaluation of our manuscript. The reviewer’s suggestions have enhanced the mechanistic depth and coherence of the review, and we have implemented each recommendation. All changes are indicated in red text in the revised manuscript.

Comment 1:

In Section 4.3, the authors note the paradox of reduced mRNA but elevated protein in diabetic kidneys. Providing a brief hypothesis on the mechanism of altered post-translational regulation in the “diabetic milieu” would show a deeper level of critical thinking. For instance, could hyperglycemia affect the glycosylation or protein stability of CN-1 independently of its genetic signal peptide efficiency?

Response 1:

We greatly appreciate this suggestion, which prompted us to think more critically about the mechanistic basis of the mRNA–protein discordance. In the revised manuscript, we have added 1–2 sentences at the end of Section 4.3 noting that the discordance may reflect altered protein stability or clearance in the diabetic milieu. For example, hyperglycemia-driven changes in N-linked glycosylation, impaired proteasomal degradation under conditions of oxidative stress and AGE accumulation, or increased uptake of circulating hepatically-secreted CN-1 by proximal tubular cells could each contribute to local protein accumulation independent of intrarenal transcription. We also note that these hypotheses are testable and should be pursued through quantitative proteomic approaches. (Revised manuscript, Section 4.3, end of paragraph)

Comment 2:

In Section 5.1, the description of carnosine acting as a “sacrificial substrate” is excellent. To improve this further, you might briefly mention if there are any known “off-target” effects of carnosine-carbonyl adducts before they are excreted, or confirm they are biologically inert.

Response 2:

Thank you for this thoughtful suggestion. We have added a sentence in Section 5.1 immediately after the mention of renal excretion, stating that carnosine-carbonyl adducts (including carnosine-methylglyoxal and carnosine-malondialdehyde conjugates) are generally considered chemically stable and biologically inert under physiological conditions, functioning as detoxification products rather than bioactive intermediates. We note, however, that systematic toxicological characterization at supraphysiological concentrations (as might occur during high-dose supplementation) has not been performed. (Revised manuscript, Section 5.1, inline addition)

Comment 3:

Consider adding a “Figure 4” that summarizes the clinical pipeline—from genetic screening to therapeutic intervention—to provide a forward-looking conclusion to the “Precision Medicine” section.

Response 3:

We sincerely appreciate this creative suggestion and gave it careful consideration. After deliberation, we concluded that adding a new figure was beyond the scope of the current revision. However, we have substantially expanded the translational discussion in Section 7.3 and the Limitations section, including a three-tiered evidence summary (well-supported, remains uncertain, critical future priorities) that serves a similar conceptual function in text form—explicitly mapping the translational arc and identifying the critical evidence gaps that must be resolved at each stage before clinical implementation can be considered. We believe this approach captures the spirit of the reviewer’s suggestion while maintaining the current figure set.

Comment 4:

The “Recent Advances” section (Section 8) mentions CNDP1 in cancer and heart failure. To prevent this section from feeling like a list of unrelated facts, add a sentence or two synthesizing why CNDP1 is relevant across these diverse pathologies. For example, explain if the common thread is the systemic regulation of carnosine’s antioxidant properties or if it is a tissue-specific metabolic vulnerability.

Response 4:

We wholeheartedly agree with this observation—the original text did read as a catalogue of disconnected findings. We have added a synthesizing paragraph after Section 8.1 that draws a unifying thread through these diverse associations. The paragraph distinguishes between two related mechanisms: a systemic antioxidant deficit mechanism (relevant to DKD and heart failure, where elevated carnosinase depletes the protective carnosine buffer in metabolically stressed tissues) and a tissue-specific metabolic vulnerability mechanism (relevant to cancer, where tumor cells may co-opt carnosinase to liberate histidine for nucleotide synthesis and pH buffering). The conclusion identifies the common denominator as the centrality of carnosine homeostasis to cellular stress responses, with downstream consequences determined by tissue-specific metabolic demands. (Revised manuscript, Section 8.1, new paragraph)

Reviewer 3 Report

Comments and Suggestions for Authors

 

Thank you for the opportunity to review the article. After reviewing it, I offer the following suggestions for improvement. These comments aim to strengthen the clarity and structure of this review.

First, clearly articulate the main objective of the review in the Introduction. Specify what new perspective or synthesis this article provides compared with prior CNDP1 or DKD reviews. Indicate the gap in the literature that this review intends to address.

Please, provide a transparent literature search strategy. Include a short section describing the review methodology, even if it is a narrative review, including the databases searched, search terms/keywords, time frame, and inclusion/exclusion criteria. This will enhance reproducibility.

Add a deeper discussion of limitations in the CNDP1 evidence base, including: inconsistent replication of genetic associations across populations; very low allele frequencies in several ancestries and their impact on clinical utility; discrepancies between CNDP1 mRNA and protein expression findings; and limited power in several population studies.

Clarify the distinction between mechanisms and hypothesis‑generating findings.

Moreover, consider shortening the mechanistic sections that repeat detailed descriptions. Expand the sections addressing translational, clinical, and precision‑medicine implications. This will increase the article's appeal.

In the article, there is also a problem with terminology consistency; hence, please standardize the use of terms such as DKD, diabetic nephropathy, CTG repeat, and Mannheim variant. 

Provide a more cautious interpretation of animal model results, acknowledging limitations in translating findings to human DKD. Discuss potential confounders affecting carnosine levels (e.g., diet, kidney function, inflammation).

Critically evaluate the robustness of existing clinical trials of carnosine supplementation, noting: small sample sizes, short durations, and limited safety data. Clarify the current developmental stage and challenges associated with carnosinase inhibitors. Differentiate clearly between promising therapeutic hypotheses and clinically validated interventions.

Provide a concise summary highlighting: what is well supported by current evidence, what remains uncertain, and specific future research directions that are most critical.

Shorten overly long sentences and remove repetitive phrasing in the entire article.

 

Author Response

We are sincerely grateful to Reviewer 3 for the thoughtful and detailed suggestions, which have substantially improved the clarity, structure, and balance of the manuscript. Several of the reviewer’s recommendations overlapped with those of Reviewer 1, and where changes address both reviewers’ concerns simultaneously, we have cross-referenced accordingly. All changes are indicated in red text in the revised manuscript.

Comment 1:

First, clearly articulate the main objective of the review in the Introduction. Specify what new perspective or synthesis this article provides compared with prior CNDP1 or DKD reviews. Indicate the gap in the literature that this review intends to address.

Response 1:

We appreciate this recommendation. The existing Introduction already describes the integrative scope of the review—synthesizing genetic, molecular, and translational evidence within a single framework. We have further clarified the review’s positioning through targeted additions: search methodology language at the end of the Introduction (defining this as a narrative review) and inline methodological caveats in Section 3.2 (framing the strengths and limitations of the CNDP1 evidence base relative to modern genomic standards). Together, these additions make clear what new perspective this review provides: an integrated, critically appraised translational synthesis incorporating the most recent advances (2024–2026) that prior reviews have not addressed. (Revised manuscript, end of Introduction and Section 3.2)

Comment 2:

Please, provide a transparent literature search strategy. Include a short section describing the review methodology, even if it is a narrative review, including the databases searched, search terms/keywords, time frame, and inclusion/exclusion criteria. This will enhance reproducibility.

Response 2:

We have added search methodology language at the end of the Introduction, explicitly identifying this as a narrative review and describing databases searched (PubMed/MEDLINE, Embase, Google Scholar), search terms, time frame (inception through January 2026), language restrictions (English), and acknowledging that no formal inclusion/exclusion criteria or risk-of-bias assessment were applied. This also addresses Reviewer 1 Comment 23. (Revised manuscript, end of Introduction)

Comment 3:

Add a deeper discussion of limitations in the CNDP1 evidence base, including: inconsistent replication of genetic associations across populations; very low allele frequencies in several ancestries and their impact on clinical utility; discrepancies between CNDP1 mRNA and protein expression findings; and limited power in several population studies.

Response 3:

We thank the reviewer for specifying these key limitations. Each has been addressed through targeted additions across the revised manuscript: (1) inconsistent replication is quantified in the inline caveats added to Section 3.2 (approximately half of ~10 studies replicated); (2) low allele frequencies and their impact on clinical utility are discussed in the new Table 1 note and in the expanded Limitations section’s health equity paragraph; (3) the mRNA–protein discrepancy is now caveated with methodological limitations (small samples, semi-quantitative IHC, no mass spectrometry) in Section 4.3; and (4) limited study power is acknowledged throughout. Additionally, a three-tiered evidence summary has been added to the Limitations section explicitly categorizing findings as “well-supported,” “remains uncertain,” and “critical priorities.” (Revised manuscript, multiple locations)

Comment 4:

Clarify the distinction between mechanisms and hypothesis-generating findings.

Response 4:

We have addressed this through inline caveats at each relevant location: Section 4.3 now identifies the mRNA–protein discordance as a hypothesis requiring validation through quantitative proteomics; Section 4.4 notes that the post-translational mechanism is demonstrated in vitro only; and Section 5.3 characterizes animal model results in the context of significant species differences. These additions ensure that readers can clearly distinguish between established biochemical properties (e.g., carnosine’s antioxidant activity, demonstrated in cell-free systems) and hypothesis-generating observations that await confirmation in human tissue or adequately powered clinical studies. (Revised manuscript, Sections 4.3, 4.4, 5.3)

Comment 5:

Moreover, consider shortening the mechanistic sections that repeat detailed descriptions. Expand the sections addressing translational, clinical, and precision-medicine implications. This will increase the article’s appeal.

Response 5:

We have expanded Sections 7.1–7.3 and the Limitations section with substantial new content addressing trial limitations, safety considerations, health equity implications, NNG/cost-effectiveness gaps, genotype-response prediction requirements, and a detailed comparison with APOL1/UMOD/SGLT2 pathway genetics. Editorial tightening to reduce repetition in the mechanistic sections has been applied throughout. We believe the revised manuscript now strikes a better balance between mechanistic exposition and translational/clinical discussion. (Revised manuscript, Sections 7.1, 7.2, 7.3, Limitations)

Comment 6:

In the article, there is also a problem with terminology consistency; hence, please standardize the use of terms such as DKD, diabetic nephropathy, CTG repeat, and Mannheim variant.

Response 6:

We have standardized terminology throughout the manuscript. “Dialbetic kidney disease” (DKD) is used as the primary term consistent with KDIGO nomenclature; “diabetic nephropathy” is retained only when citing studies that used this specific term. “Mannheim variant” refers specifically to the (CTG)₅ allele, while “(CTG)ₙ repeat” is used for the polymorphism in general. “Carnosinase-1” and its abbreviation “CN-1” are used consistently throughout.

Comment 7:

Provide a more cautious interpretation of animal model results, acknowledging limitations in translating findings to human DKD. Discuss potential confounders affecting carnosine levels (e.g., diet, kidney function, inflammation).

Response 7:

We have added 1–2 sentences in Section 5.3 explicitly discussing the critical species difference: mice do not express serum carnosinase-1 in circulation (lacking the CNDP1 signal peptide), resulting in inherently higher baseline carnosine levels that limit direct translational inference. This also addresses Reviewer 1 Comment 6. Regarding confounders: dietary carnosine intake (meat consumption is a major exogenous source), kidney function (affecting carnosine clearance), systemic inflammation, and age/sex effects are all relevant confounders that can influence carnosine levels independently of genotype and should be controlled for in future studies. (Revised manuscript, Section 5.3, inline addition)

Comment 8:

Critically evaluate the robustness of existing clinical trials of carnosine supplementation, noting: small sample sizes, short durations, and limited safety data. Clarify the current developmental stage and challenges associated with carnosinase inhibitors. Differentiate clearly between promising therapeutic hypotheses and clinically validated interventions.

Response 8:

We have added trial caveats in Section 7.1 covering sample sizes (n = 90 for the largest renal trial), short durations (12 weeks maximum), absence of post-treatment follow-up, no adjustment for regression to the mean, unreported background therapy, and lack of independent replication. The Section 7.2 addition states that no phase I trials of carnostatine have been initiated and flags unresolved PK and safety questions. The expanded Limitations section draws an explicit distinction between “therapeutic hypothesis (genetically and mechanistically plausible)” and “clinical reality (unproven in adequately powered human trials).” This also addresses Reviewer 1 Comments 12–17. (Revised manuscript, Sections 7.1, 7.2, Limitations)

Comment 9:

Provide a concise summary highlighting: what is well supported by current evidence, what remains uncertain, and specific future research directions that are most critical.

Response 9:

We have added a three-tiered evidence summary in the expanded Limitations section. Well-supported: in vitro functional consequences of the CTG repeat, carnosine-mediated cytoprotection in cell culture, animal model validation, and European-ancestry genetic association. Remains uncertain: non-European replication, magnitude of human genetic protection (likely inflated), significance of kidney expression changes, biomarker predictive value, and clinical trial reproducibility. Critical priorities: multi-ethnic GWAS and MR studies, genotype-stratified trials with hard renal endpoints, first-in-human carnosinase inhibitor studies, and identification of alternative risk variants for non-European populations. (Revised manuscript, Limitations section, final paragraph)

Comment 10:

Shorten overly long sentences and remove repetitive phrasing in the entire article.

Response 10:

We have performed editorial revision throughout the manuscript to shorten overly long sentences, eliminate redundant phrasing, and improve overall readability.

Round 2

Reviewer 2 Report

Comments and Suggestions for Authors

all reviewer suggestions were addressed

Reviewer 3 Report

Comments and Suggestions for Authors

Thank you very much for your thorough and thoughtful revisions. I have carefully reviewed your detailed point‑by‑point responses and the updated manuscript. I sincerely appreciate the substantial work you invested in addressing all comments.

The revisions have clearly improved the clarity, structure, and balance of the manuscript. The strengthened Introduction, enhanced methodology description, expanded Limitations section, refined mechanistic caveats, and improved translational framing successfully resolve all previously identified issues. Terminology is now consistent, and the revised text reads smoothly and coherently.

I am fully satisfied with the current version of the manuscript and have no further comments or suggestions.

Thank you once again for your careful and constructive work.