Diabetes mellitus and the risk of ovarian cancer: an updated systematic review and meta-analysis of cohort and case-control studies.

A total of 3,720 records was identified via database searches alongside an additional 8 records discovered via hand-searching or bibliographic screening. This process yielded 3,564 unique records following the removal of duplicates. After conducting a thorough screening of the titles and abstracts, a total of 168 full-text articles were evaluated for their eligibility. Afterwards, 125 studies were excluded for various reasons, including insufficient outcome data, irrelevant exposure definitions or unrelated study design. Finally, a total of 43 studies were incorporated into the systematic review and meta-analysis, which included 30 cohort studies and 13 case–control studies (Fig. 1 ) [ 21 , 28 – 69 ] (Table 1 ). Study-level characteristics are summarized in Tables 2 and 3 , and the PECOT specification is provided in Table 1 . Lastly, Study-specific covariate sets for the included estimates, or the corresponding standardization factors for ratio-based reports, are presented in Supplementary Table S2. Fig. 1 PRISMA 2020 flow diagram for Updated Diabetes Mellitus and Ovarian Cancer systematic review PRISMA 2020 flow diagram for Updated Diabetes Mellitus and Ovarian Cancer systematic review Table 1 PECOT structure for research question Criteria Description Population Women with and without a history of diabetes mellitus included in observational studies (cohort and case–control) assessing ovarian cancer incidence. Exposure A history of diabetes mellitus, including type 1, type 2, and gestational diabetes. Comparison Women without a history of diabetes mellitus Primary Outcome The incidence of ovarian cancer Type of Studies Observational studies including cohort and case-control studies Inclusion Criteria Original observational studies (cohort or case–control) that assessed the association between diabetes mellitus and the risk of ovarian cancer in human populations and reported a risk estimate (e.g., RR, OR, HR) or provided sufficient data to calculate it. Exclusion Criteria Randomized controlled trials, reviews, meta-analyses, letters, editorials, case reports, animal studies, and studies lacking sufficient data to estimate the association between diabetes mellitus and ovarian cancer risk. Search Terms “Diabetes mellitus”, “Type 1 diabetes”, “Type 2 diabetes”, “Gestational diabetes”, “Ovarian cancer”, “Ovarian neoplasms”, “Cohort studies”, “Case-control studies”, and their synonyms identified through Thesauruses, Emtree, and MeSH terms. Databases PubMed, Embase, Scopus, Web of Science, Cochrane Library PECOT structure for research question Table 2 Baseline characteristics of included studies (Cohort) Baseline characteristics of included studies (Cohort) Table 3. Baseline characteristics of included studies (Case-Control) Baseline characteristics of included studies (Case-Control) Using a random-effects model with the restricted maximum likelihood (REML), the pooled relative risk (RR) of ovarian cancer associated with diabetes mellitus across 46 studies was 1.14 (95% CI, 1.02–1.27), indicating a modest but statistically significant increase in risk (Fig.  2 ). Between-study heterogeneity was (I² = 88.35%), which was considered to be substantial, therefore supporting the choice of implementing a random-effects model. I² remained high across most strata, indicating that inconsistency was not resolved by single-factor subgrouping. Patterns were compatible with variability in exposure definition and outcome ascertainment as well as regional differences in background risk and adjustment structures (Table 4 ). In sensitivity analyses restricted to cohort designs and to multivariable-adjusted estimates (preferably hazard ratios), the association remained directionally consistent (Table 4 ). Additionally, leave-one-out sensitivity analysis did not significantly shift the pooled estimate with no specific study disproportionately affecting the overall effect size (Fig.  2 ). Methodological sensitivity analyses were directionally consistent across design, adjustment, study quality, and follow-up strata. Within-subtype sensitivity analyses were likewise concordant. For transparency, stratum-specific Leave-one-out panels are provided in the Supplement; across all strata and diabetes subtypes, omitting any single study did not materially alter the stratum summary (Supplementary Figure S1−9). Furthermore, in univariate meta-regressions, no evidence of modification by study-level age (slope on log RR β = −0.00006, SE 0.00452, p  = 0.989), follow-up duration (β = 0.00466, SE 0.00699, p  = 0.506), or study quality (NOS points; β = 0.01073, SE 0.05423, p  = 0.843) was observed; model R-squared was 0% in all cases. Bubble plots are shown in Supplementary Figures S10–S12, and numerical outputs are summarized in Supplementary Table S1. Fig. 2 Forest plot of the association between Diabetes Mellitus and Ovarian Cancer and Leave-one-out sensitivity analysis Forest plot of the association between Diabetes Mellitus and Ovarian Cancer and Leave-one-out sensitivity analysis Subgroup analyses were prespecified by age, adjustment status, BMI adjustment, follow-up duration, study quality (NOS), diabetes subtype, setting, geographic region, and study design. Estimates were broadly consistent with the primary association. By age, the pooled RR was 1.28 (95% CI, 1.07–1.52) for < 55 years and 1.07 (0.91–1.27) for ≥ 55 years. Adjusted studies yielded RR = 1.18 (1.05–1.33) versus 0.94 (0.68–1.31) in unadjusted analyses. For BMI-adjusted versus non-adjusted models, RRs were 1.33 (0.86–2.06) and 1.12 (1.00–1.26), respectively. With ≥ 10 years of follow-up, RR was 1.20 (1.04–1.37) versus 1.08 (0.88–1.32) for < 10 years. By study quality, RRs were 0.84 (0.60–1.17) for NOS ≤ 5, 1.11 (0.66–1.87) for NOS = 6, and 1.18 (1.05–1.32) for NOS ≥ 7. By diabetes subtype, pooled RRs were 1.46 (1.04–2.05) for type 1, 1.12 (0.97–1.29) for type 2, 1.09 (0.93–1.27) for gestational, and 0.90 (0.50–1.61) for unspecified. Population-based studies showed RR = 1.18 (1.06–1.31) versus 1.04 (0.78–1.39) in hospital-based designs. Regionally, Europe (RR = 1.10, 0.95–1.29), America (0.88, 0.69–1.13), Asia (1.36, 1.08–1.71) and Australia (1.22, 1.14–1.29) differed (Table 4 ). Table 4 Subgroup Meta-analysis Variables Category No. study Pooled RR (%95 CI) Heterogeneity assessment between studies Heterogeneity assessment between subgroup Publication bias assessment Overall 46 1.14(1.02,1.27) I 2 (%) P-value Q P-Value B SE P-value 88.35 < 0.001 0.48 0.416 0.24 Age not reported 8 1.04(0.76,1.40) 91.47 < 0.001 2.5 0.29 ≥ 55 19 1.07(0.91,1.27) 91.48 < 0.001 < 55 19 1.28(1.07,1.52) 59.07 < 0.001 Adjustment 1.63 0.2 Yes 35 1.18(1.05,1.33) 79.96 < 0.001 No 11 0.94(0.68,1.31) 97.10 < 0.001 BMI 0.57 0.45 Yes 7 1.33(0.86,2.06) 70.28 < 0.001 No 39 1.12(1.00,1.26) 88.48 < 0.001 Follow-up 0.7 0.4 ≥ 10 24 1.20(1.04,1.37) 82.21 < 0.001 < 10 22 1.08(0.88,1.32) 92.66 < 0.001 NOS 3.61 0.16 ≤ 5 5 0.84(0.60,1.17) 54.89 0.07 6 6 1.11(0.66,1.87) 87.58 < 0.001 ≥ 7 35 1.18(1.05,1.32) 84.98 < 0.001 Population 2.97 0.4 T1DM 6 1.46(1.04,2.05) 73.00 0.01 T2DM 31 1.12(0.97,1.29) 91.73 < 0.001 GDM 7 1.09(0.93,1.27) 0.00 0.34 DM 2 0.90(0.50,1.61) 82.94 0.02 Population setting 0.64 0.42 PB 38 1.18(1.06,1.31) 86.43 < 0.001 HB 14 1.04(0.78,1.39) 81.01 < 0.001 Region 8.41 0.04 EU 20 1.10(0.95,1.29) 85.57 < 0.001 America 7 0.88(0.69,1.13) 60.42 0.02 Asia 17 1.36(1.08,1.71) 89.07 < 0.001 Australia 3 1.22(1.14,1.29) 0.01 0.48 Study type 1.4 0.24 Cohort 33 1.18(1.05,1.34) 89.87 < 0.001 Case-Control 13 1.00(0.78,1.28) 67.19 < 0.001 ‘Adjusted’ denotes the most fully adjusted overall estimate per study; ‘Time-to-event’ refers to hazard-ratio–based estimates where available Subgroup Meta-analysis ‘Adjusted’ denotes the most fully adjusted overall estimate per study; ‘Time-to-event’ refers to hazard-ratio–based estimates where available In interpreting the summary association for ‘diabetes’, it should be noted that most included effect sizes pertain to T2D; accordingly, the overall estimate is largely informed by T2D, with smaller contributions from T1D and GDM. Subtype-specific pooled estimates are provided in Table 4  and should be preferred for etiologic interpretation. For subgrouping, one study conducted across both the EU and Australia was entered twice, once under each region, so that each record contributed only to its respective regional stratum. Similarly, six studies that included both population-based (PB) and hospital-based (HB) samples were duplicated such that each copy contributed to a single setting (PB or HB). These duplications were applied solely within the relevant subgroup analyses and did not alter the overall pooled estimate. Egger’s regression test did not indicate small-study effects: the intercept (B) was 0.48 (SE 0.416; p  = 0.24), consistent with no evidence of publication bias among the included studies (Table 4 ). These findings suggest that the pooled association is unlikely to be materially influenced by selective reporting of smaller studies.

This study has been taken out as an updated systematic review and meta-analysis alongside being conducted in strict adherence to the PRISMA guidelines [ 26 ]. The corresponding protocol was prospectively registered on the Open Science Framework (10.17605/OSF.IO/MVQKJ) [ 27 ]. This research serves as an update to a prior meta-analysis conducted by Wang et al. [ 19 ], integrating seven newly identified studies [ 21 , 28 – 33 ] and employing enhanced subgroup and sensitivity analyses. A thorough search was conducted in literature within PubMed/MEDLINE, Embase and the Cochrane Library; covering the entire span of these databases from their inception to the present alongside a focus on publications in the English language. This study utilized controlled-vocabulary headings alongside free-text terms related to diabetes mellitus, including all major subtypes, and ovarian cancer. These were integrated with study-design filters to effectively identify relatable cohort and case-control studies. To ensure the inclusion of studies which were not identified through electronic means, the reference lists of all full-text articles were meticulously hand-searched by two independent reviewers. Titles and abstracts of found studies underwent a duplicate screening process, followed by a thorough review of full-text articles based on previously established inclusion criteria. Titles and abstracts plus full texts were screened independently and in duplicate by two reviewers (BG and SA); disagreements were resolved by discussion, with a third reviewer (YM) acting as adjudicator when consensus was not reached. These criteria mandated an observational design involving human populations, an assessment of the relationship of diabetes mellitus, regardless of the subtype, with the incidence of ovarian cancer, and finally the availability of quantitative risk estimates or adequate data to derive such estimates from extracted data. Discrepancies were addressed through comprehensive discussions between the two reviewers and when necessary, a thirds reviewer was consulted to ensure the consistency alongside minimizing the potential bias in inclusion. Data extraction was performed independently and in duplicate by two reviewers (BG and SA) using a piloted form; discrepancies were reconciled by discussion, and unresolved items were adjudicated by a third reviewer (BM). The extracted data included study design characteristics, participant demographics, the specific diabetes subtype examined, reported risk estimates and the adjustment factors utilized. Since this review updates prior syntheses, the PECOT framework prespecified the exposure as diabetes mellitus irrespective of study design, and both cohort and case–control studies were eligible. When multiple estimates were reported, the most fully adjusted overall estimate was extracted (the exact covariates (or standardization factors) for each included estimate are listed in Supplementary Table S2.); furthermore, time-to-event (hazard ratio) models were preferred where available. The final dataset underwent a thorough cross-checking process by the two reviewers, which was in order to guarantee the consistency and to reduce the potential for errors within this process. Risk of bias was assessed independently by two reviewers (BG and SA) using the Newcastle–Ottawa Scale; disagreements were resolved through consensus with third-reviewer adjudication when required (YM) [ 25 ]. This method allocates a maximum of nine stars across the domains of selection, comparability and outcome/exposure. Included research studies were classified into three categories based on quality; low quality (≤ 5 stars), moderate quality (6 stars) and high quality (≥ 7 stars). Following the cross-checked quality assessment of included studies by two reviewers, these classifications were utilized in subsequent subgroup analyses. Meta-analytic pooling was undertaken in Stata 18 using random-effects models fitted with the restricted maximum likelihood (REML) estimator. Study-specific effects were transformed to the log scale and combined to estimate relative risks (RR). Because ovarian cancer is relatively uncommon, differing association measures reported across studies were regarded as providing comparable approximations of RR [ 1 ]. Anticipated clinical and methodological diversity was accommodated by estimating the between-study variance (τ²) via REML. Heterogeneity was evaluated with Cochran’s Q and summarized with I². Potential small-study effects were appraised using Egger’s regression test. Methodological sensitivity analyses were prespecified for study design (cohort vs. case–control), adjustment status (multivariable vs. less-adjusted), study quality (Newcastle–Ottawa Scale categories), and follow-up duration (< 10 vs. ≥ 10 years) and were repeated, where data permitted, within diabetes subtypes (T1D, T2D, GDM). Leave-one-out diagnostics were performed only as supplementary checks within each stratum and subtype. Lastly, exploratory univariate meta-regressions (REML) were conducted to assess study-level modifiers; age, follow-up duration, and study quality. Since BMI adjustment was inconsistently coded across included records, its impact was evaluated primarily via methodological sensitivity strata (adjusted vs. less-adjusted). Between-study heterogeneity was explored a priori using subgroup analyses for design, quality, region, age, follow-up, population setting, diabetes subtype, and adjustment patterns. In addition, variability in exposure definition (e.g., self-report, clinical/administrative records, antidiabetic medication use) and outcome ascertainment (registry/medical records versus self-report) was considered as potential sources of inconsistency. The primary exposure was predefined as diabetes mellitus irrespective of subtype to maintain comparability across studies. Subtype-specific analyses for type 1 diabetes (T1D), type 2 diabetes (T2D), and gestational diabetes mellitus (GDM) were prespecified a priori. The overall ‘diabetes’ estimate therefore represents a weighted average across subtypes and, given the composition of the evidence base, is expected to be driven primarily by T2D. Subgroup analyses were prespecified by participant age (< 55 years vs. ≥55 years vs. not specified), adjustment status and BMI adjustment (yes/no), diabetes subtype (gestational, type 1, type 2, unspecified), study design, follow-up duration (< 10 years vs. ≥10 years), population setting (population-based vs. hospital-based), and geographic region (Europe, Asia, America, Australia); where data permitted, variability in exposure definition and outcome ascertainment was also considered.

The present study, being a systematic review and meta-analysis of observational studies, highlights a modest, yet statistically significant, association between diabetes mellitus and the risk of ovarian cancer development. Despite the magnitude of this association being small, a biologically plausible link is supported; although this association is likely to be influenced by competing hormonal, reproductive and lifestyle factors. The consistency of the observed effect across various study designs, populations and analytical methods suggests that diabetes mellitus could hold a collective role with regards to ovarian carcinogenesis. However, the risk associated with diabetes mellitus is notably lower compared to other linked malignancies, such as endometrial or pancreatic cancer. While statistically significant, the association was found to be modest in relative terms and the corresponding absolute risk increase at the population level is likely small. Although these findings do not justify changes to be made to clinical practice or screening guidelines, they emphasize the emergent importance of metabolic health consideration within broader strategies regarding cancer prevention. Future research, including studies which incorporate molecular subtypes, longitudinal glycemic assessments and treatment exposures, is therefore of most importance to unravel the precise etiological role of diabetes mellitus in ovarian cancer development alongside exploring targeted interventions for risk mitigation.

Diabetes was associated with a small but statistically significant increase in ovarian cancer risk (RR 1.14, 95% CI 1.02–1.27); sensitivity analyses gave similar results. Heterogeneity was high (I² 88%), likely reflecting differences in populations, exposure/outcome definitions, and confounding; Egger’s test did not indicate small-study effects. The signal appeared stronger for type 1 diabetes, while type 2 and gestational diabetes showed smaller or null averages; absolute risks remain low. These findings do not justify changes to screening; priorities include histotype-resolved analyses and direct metabolic measures alongside diabetes status. Diabetes was associated with a small but statistically significant increase in ovarian cancer risk (RR 1.14, 95% CI 1.02–1.27); sensitivity analyses gave similar results. Heterogeneity was high (I² 88%), likely reflecting differences in populations, exposure/outcome definitions, and confounding; Egger’s test did not indicate small-study effects. The signal appeared stronger for type 1 diabetes, while type 2 and gestational diabetes showed smaller or null averages; absolute risks remain low. These findings do not justify changes to screening; priorities include histotype-resolved analyses and direct metabolic measures alongside diabetes status. Diabetes perturbs insulin and glucose signaling, promotes low-grade inflammation, and alters lipid and hormone pathways—mechanisms that plausibly influence ovarian carcinogenesis [ 70 ]. In this REML random-effects synthesis, diabetes was associated with a modest but statistically significant elevation in risk. The effect persisted across analytic choices and in higher-quality cohorts, arguing against artefact, yet substantial heterogeneity across populations, measurements, and co-exposures tempers generalization. With many contributing studies, leave-one-out diagnostics are intrinsically uninformative; the stratum-specific leave-one-out checks confirmed that no individual study dominantly influenced the pooled estimates within any methodological stratum or diabetes subtype. The biological and clinical distinctions among diabetes subtypes are recognized. In order to avoid obscuring these differences, subtype-specific pooled estimates are reported alongside the overall estimate, and readers are cautioned that the latter is a weighted average dominated by T2D because of study mix. Retaining an overall estimate preserves continuity with prior literature and facilitates high-level synthesis, whereas subtype-resolved results better reflect etiologic specificity. Findings from this update align directionally with prior syntheses that reported small, positive associations between diabetes and ovarian cancer, while estimates varied across reviews because of differences in case mix, exposure and outcome ascertainment, and the extent of confounder control [ 19 , 24 ]. By incorporating additional contemporary cohorts and prespecified subgroup analyses, the present study refines the pooled estimate without altering the overall message that any association is modest on average and heterogeneous across contexts. The observed inconsistency is plausibly driven by definition and measurement variability. Diabetes exposure was ascertained through self-report, clinical or administrative records, and sometimes by medication proxies, each carrying differing risks of non-differential misclassification that can dilute or inflate effects. Outcome ascertainment also varied, with reliance on registries, medical records, or self-report, and occasional inclusion of borderline tumors or related primary peritoneal neoplasms, introducing scope for outcome misclassification. Region-specific confounding structures—reflecting differences in reproductive and hormonal histories, adiposity distributions, diagnostic and coding practices, and access to care—further diversify estimates despite multivariable adjustment. These considerations align with the persistence of high I² across strata. Lastly, exploratory meta-regressions did not identify study-level age, follow-up length, or NOS score as contributors to between-study variability, indicating that these factors are unlikely to explain the observed heterogeneity. Two features of this analysis strengthen credence in the overall association. First, use of REML to estimate the between-study variance provided a principled way to accommodate genuine dispersion in effects across diverse designs, settings and eras, yielding confidence intervals that reflect that dispersion rather than treating all studies as near-identical. Second, influence diagnostics showed that no single study unduly determined the pooled estimate; the association held when each study was removed in turn, which argues against a “house of cards” effect where one highly weighted outlier drives the result [ 71 ]. Equally important is what was not seen: Egger’s regression test did not indicate small-study effects, reducing concern that selective reporting among smaller or early studies explains the finding. Interpreting a small relative risk requires attention to clinical scale [ 71 ]. Ovarian cancer remains a comparatively uncommon malignancy, and even a 10–15% relative difference translates into a limited absolute excess for most individuals [ 72 ]. Contemporary global data underscore that ovarian cancer accounts for a minority of incident cases worldwide, with age-standardized incidence substantially lower than that of breast, colorectal, or lung cancers; this context helps anchor the finding in absolute terms [ 4 ]. Moreover, major guideline bodies continue to advise against population screening for ovarian cancer in asymptomatic, average-risk women because currently available tests do not reduce mortality and can produce meaningful harm through false positives and unnecessary surgery [ 73 ]. Accordingly, diabetes status alone should not alter screening or surveillance practices; rather, it is best understood as one component within a broader constellation of risk determinants that remains dominated by reproductive history, genetic predisposition, and gynecologic conditions [ 74 ]. The biological coherence of a modest association is credible. Chronic hyperinsulinemia, hyperglycemia, and low-grade inflammation can activate mitogenic insulin/insulin-like growth factor signaling, intersect with PI3K–AKT–mTOR and MAPK cascades, and promote oxidative DNA damage, collectively creating a tissue milieu that may favor tumor initiation and progression [ 75 – 77 ]. These mechanisms are consistent with small, cumulative shifts in risk that vary with exposure intensity, duration, and tissue susceptibility rather than with large organ-specific effects, and experimental and epidemiologic data on insulin/IGF signaling in other cancers provide additional plausibility without guaranteeing a uniform effect in ovarian tissue [ 78 ]. Patterns within the evidence hint at where heterogeneity may arise, even when formal tests for between-group differences do not always reach statistical significance [ 79 ]. The association appeared more apparent in cohorts than in case–control designs, a contrast that is methodologically intuitive [ 19 ]. Prospective cohorts ascertain diabetes before cancer develops, typically with stronger capture of covariates and clearer temporal ordering; case–control studies, by contrast, must reconstruct past exposure and may be more vulnerable to selection or recall biases [ 80 ]. Additionally, population-based sampling frameworks tended to indicate more coherent associations when compared to hospital-based samples, possibly reflecting better generalizability plus reduced selection regarding care-seeking behaviors [ 81 ]. These gradients suggest that study architecture matters for signal detection when the true effect is small [ 81 ]. Age patterns were suggestive rather than definitive. A relatively stronger association in younger women and attenuation at older ages could reflect longer windows of exposure to metabolic perturbations, different distributions of diabetes phenotype or dilution by competing risks in later life [ 82 ]. Yet because ovarian cancer incidence rises with age, absolute differences will still be modest for most individuals, underscoring the need to frame results in both relative and absolute terms [ 83 ]. Similar caution applies to adjustment patterns. Adjusted analyses more consistently detected an association than crude analyses, which may mean that unadjusted estimates are noisy rather than that confounding is driving a spurious positive result; the direction of confounding in this literature can be complex because some reproductive and hormonal determinants of ovarian cancer correlate with adiposity or insulin resistance in ways that may either mask or accentuate the underlying diabetes signal if left uncontrolled [ 83 ]. Adiposity deserves special consideration. In models without explicit BMI adjustment, the pooled association was small but leaned positive; in BMI-adjusted strata, estimates were compatible with both small harm and no effect, with wide uncertainty. Because BMI is an imperfect surrogate for metabolic health and cannot fully represent ectopic adiposity, chronic inflammation, or hyperinsulinemia attenuation after BMI adjustment does not necessarily imply that obesity “explains away” the diabetes–ovarian cancer link [ 83 ]. It is equally plausible that diabetes and adiposity travel together yet exert overlapping and partially independent effects through shared and distinct pathways [ 84 ]. The upshot for interpretation is modest; diabetes likely signals a composite of metabolic disturbances of which excess adiposity is a central but not exclusive component [ 84 ]. Duration of follow-up offered another window on temporality. Associations that were clearer in studies with at least a decade of follow-up are consistent with a latency process in which sustained metabolic dysregulation takes time to influence tumor initiation or progression. They also argue, albeit indirectly, against the entire signal being an artifact of diagnostic intensity immediately after diabetes diagnosis, because ovarian cancer lacks an effective screening paradigm that would produce large short-term detection spikes [ 19 ]. In contexts where surveillance does occur, it is usually symptom-driven rather than population-based, which reduces the likelihood that early diagnostic behavior alone explains a persistent association over extended follow-up [ 85 ]. Geography emerged as the only subgroup where between-region differences achieved conventional statistical significance, with higher relative risks observed in Asia and Australia, a near-null pattern in Europe, and lower estimates in America. Several non-exclusive explanations are plausible; background distributions of reproductive and hormonal exposures, parity, age at menarche and menopause, oral contraceptive use, menopausal hormone therapy, endometriosis, differ by region and could interact with metabolic factors to modify risk [ 19 ]. Environmental and lifestyle patterns pertinent to metabolic health, including diet and adiposity trajectories across the life course, also vary geographically [ 86 ]. Genomic backgrounds and differences in healthcare access or diagnostic pathways may contribute further [ 87 ]. It is equally possible that regional contrasts partly reflect differences in study design, covariate capture and data completeness. These explanations remain hypotheses within the current evidence base; they nonetheless align with the understanding that ovarian cancer is not a single disease entity and that risk factors may show histotype-specific or context-specific associations [ 88 ]. Diabetes subtype patterns add another layer of nuance. A higher pooled estimate for type 1 diabetes than for type 2 or gestational diabetes, while based on fewer studies, is not inconsistent with biological expectations [ 19 , 89 ]. Autoimmune inflammation, earlier age of onset, and longer cumulative exposure to exogenous insulin could, in principle, shape risk differently from the predominantly insulin-resistant, adiposity-linked phenotype of type 2 diabetes [ 39 ]. The gestational diabetes signal, by contrast, was compatible with little to no long-term effect on average, which may reflect the transient nature of the metabolic disturbance for many women; however, it should be acknowledged that gestational diabetes can mark a trajectory toward later type 2 diabetes in some, and the time horizon of follow-up will influence what is observed [ 19 ]. Across subtypes, wide intervals and heterogeneity caution against over-interpretation; the more reliable conclusion is that the diabetes–ovarian cancer association, when present, is likely modest and heterogeneous rather than uniform in size or mechanism. One practical issue in the subgroup work merits brief mention because it clarifies how strata were constructed [ 90 ]. A study conducted across both the European Union and Australia was entered twice for regional analyses, once in each geographic stratum, so that regional estimates would not be conflated [ 39 ]; similarly, six studies that included both population-based and hospital-based samples were duplicated within the setting subgroup so that each copy contributed only to its relevant stratum [ 48 , 52 , 53 , 65 , 68 ]. These analytic choices were confined to subgroup analyses and did not alter the overall pooled estimate; they simply allowed strata to reflect their labels faithfully. The broader epidemiologic architecture of ovarian cancer helps explain why a small diabetes-related shift may be detectable yet remains clinically modest [ 90 ]. Epithelial ovarian cancer encompasses distinct histotypes with different cells of origin, molecular signatures, and risk profiles; high-grade serous tumors dominate incidence and have risk patterns that differ from endometrioid, clear cell, or mucinous tumors [ 91 ]. Risk models that ignore histotype can dilute or obscure associations that are subtype-specific [ 91 ]. Where subtype-specific patterns have been reported, metabolic exposures appear most relevant for endometrioid and, to a lesser extent, clear cell tumors, which align with estrogenic and inflammatory pathways and the endometriosis-associated etiology seen in parts of this spectrum [ 1 , 5 ]. Associations for high-grade serous disease are less consistent, and mucinous tumors often show weaker or different correlations, such as with smoking, that are not overtly metabolic [ 1 , 5 ]. Against this backdrop, any diabetes-related signal would be expected to concentrate in histotypes with stronger links to adiposity and insulin–IGF signaling; future studies should therefore priorities histotype-resolved analyses that incorporate direct measures of adiposity and insulin resistance alongside diabetes status. Subtype-resolved data on diabetes were limited or inconsistently reported, likely contributing to heterogeneity and potentially masking sharper signals in particular histotypes. Interpreting a small average effect against a biologically heterogeneous outcome is therefore appropriate. Observational synthesis of small effects is vulnerable to design choices, exposure and outcome misclassification, and incomplete control of confounding. Diabetes definitions ranged from self-report to administrative codes with inconsistent subtype separation, and granular data on glycemic control, duration, and treatment were often absent. Ovarian cancer classification has also evolved, leaving some legacy datasets misaligned with current histotype taxonomies [ 92 ]. Non-differential misclassification would attenuate associations, and short-term diagnostic intensity around diabetes diagnosis could bias estimates; the clearer associations in longer follow-up are less consistent with such short-lived artefacts [ 92 ]. From a pragmatic standpoint, these findings should be integrated into clinical conversations with proportion and clarity. Diabetes is a common condition with broad implications for vascular, renal, and neurologic outcomes; any incremental cancer risk acts alongside those dominant concerns rather than supplanting them [ 93 ]. For ovarian cancer specifically, established determinants, including inherited susceptibility (such as BRCA1/2), family history, parity and contraceptive history, and certain gynecologic conditions, remain the principal drivers of individual risk assessment and counseling [ 83 ]. In average-risk, asymptomatic women, there is no role for ovarian cancer screening, and the present results do not alter that guidance [ 73 ]. Instead, diabetes may be viewed as a modest, context-dependent risk signal that contributes to a multifactorial picture and is most informative when interpreted alongside reproductive, hormonal, and genetic factors rather than in isolation [ 83 ]. Although a statistically significant association between diabetes mellitus and ovarian cancer risk was observed in the present study, the absolute increase in risk attributable to diabetes is likely to be small in most populations, given the low baseline incidence of ovarian cancer [ 1 ]. Consequently, the present findings should be regarded as contributory to the etiologic understanding of ovarian carcinogenesis and as supportive of comprehensive strategies to improve metabolic health, rather than as evidence warranting modifications of existing ovarian cancer screening recommendations for women with diabetes. Within the broader landscape of cancer prevention, these results are most appropriately interpreted as reinforcing the importance of integrated approaches to metabolic risk reduction that are expected to yield benefits across multiple cancer sites and cardiovascular outcomes. Finally, in considering why a modest association emerges more clearly in some contexts than others, it helps to return to first principles. Metabolic dysregulation is a diffuse exposure that intersects with multiple carcinogenic pathways and with life-course factors that differ by geography, cohort era, and healthcare systems [ 84 ]. Ovarian cancer itself is a set of diseases with heterogeneous origins and pathobiology [ 88 ]. Against that backdrop, small, directionally consistent signals are exactly what would be expected when a ubiquitous exposure exerts a limited, tissue-contingent influence [ 94 ]. The present synthesis, by applying REML to accommodate dispersion, by favoring prospective and population-based evidence where available, and by probing robustness through influence analyses, delineates such a signal without overstating its magnitude. It supports the view that diabetes is linked to a slight elevation in ovarian cancer risk that is real at the population level, heterogeneous across contexts, and small in absolute terms for most individuals; an interpretation that fits comfortably within current knowledge about disease burden, screening policy, and the biology of insulin/IGF signaling and inflammation [ 72 ].

While this meta-analysis employs a robust methodological framework and incorporates a substantial body of observational data, several limitations should be acknowledged. Still, residual confounding remains a significant concern, since the adjustment for critical variables such as parity, use of oral contraceptive use, history of hormone therapy and other comorbidities was found to be wide-ranging among the included studies. Restricting the synthesis to adjusted, cohort-based time-to-event estimates was considered, but doing so would diminish continuity with earlier updates and materially reduce study coverage. Instead, prespecified strata by design and adjustment status are presented to gauge the impact of potential confounding and design differences; the convergence of cohort-only and multivariable-adjusted strata with the primary model supports robustness. Nevertheless, residual confounding cannot be excluded, and future studies using standardized time-to-event reporting and harmonized adjustment sets remain a priority. Inconsistent classifications of diabetes mellitus, along with insufficient data on disease duration, glycemic control, and pharmacologic treatments, further complicate the interpretation of the findings. The impact of specific diabetes medications, such as metformin and exogenous insulin, on ovarian cancer risk is likely to differ, but the lack of stratification by treatment modality presents a considerable limitation. Available observational evidence remains limited and heterogeneous. A nationwide cohort from Taiwan reported lower ovarian cancer incidence among metformin users with type 2 diabetes, while other settings have yielded small or null associations; signals suggesting higher risk with exogenous insulin or sulfonylureas derive largely from older datasets with constrained control for confounding and surveillance bias [ 32 , 33 , 66 , 68 ]. Recent narrative and umbrella reviews conclude that medication-specific effects are biologically plausible yet unproven, underscoring the need for analyses with time-updated exposure, dose–duration metrics, and concurrent measures of glycemic control [ 15 , 16 , 23 ]. Additionally, the absence of histologic subtype data means that the results may not fully capture potential differences in ovarian cancer subtypes, limiting both the accuracy and generalizability of the findings. Finally, variability in diabetes exposure definitions and ovarian cancer ascertainment across studies, together with region-specific confounding structures, likely contributed to the high between-study heterogeneity observed. Moreover, stratified analyses regarding ovarian cancer histotype and specific diabetes treatment modalities could not be undertaken, as such information was infrequently and inconsistently reported across included studies, thus limiting the mechanistic insight which could be derived from the present synthesis. It is believed that future research should aim to address the mentioned limitations through prospective cohort studies which hold standardized definitions regarding both diabetes mellitus and ovarian cancer. Furthermore, detailed phenotyping of exposures like subtypes of diabetes alongside treatment regimens, aside from adjustments for confounding factors, would further enrich the precision regarding the risk assessments. In particular, future collaborative studies that harmonize definitions of diabetes exposure and treatment modalities across cohorts and integrate molecular plus phenotypic tumor data would be expected to reduce residual heterogeneity and allow more refined characterization of risk patterns. Moreover, it is believed that stratifying analyses by ovarian cancer histologic subtype would provide a more nuanced understanding of the association; potentially revealing tissue-specific effects. On the other hand, meta-analyses regarding individual participant data, mechanistic studies focused on the tissue-specific effects of hyperinsulinemia and glycemic dysregulation on ovarian carcinogenesis are of necessity to further elucidate the underlying biological mechanisms. With the limitations outlined, it is suggested for the modest association detected in the present study should be interpreted with caution.

Ovarian cancer (OC) remains a leading cause of gynecologic cancer mortality and is frequently diagnosed at advanced stages, limiting opportunities for early intervention and contributing to poor survival [ 1 – 4 ]. Diabetes mellitus (DM) is highly prevalent and characterized by chronic hyperglycemia, insulin resistance, and low-grade inflammation, creating systemic conditions that may plausibly influence carcinogenesis in hormonally responsive tissues [ 5 – 9 ]. Clarifying whether DM confers an increased risk of OC is relevant to public health and clinical counselling, yet the strength and consistency of any association have remained uncertain. Mechanistic links between DM and cancer have been proposed, including hyperinsulinemia and insulin/insulin-like growth factor signaling, cross-talk with PI3K–AKT–mTOR and MAPK cascades, adiposity-related steroidogenesis, and pro-inflammatory pathways that can modulate tumor initiation and progression [ 5 – 9 ]. Because OC comprises biologically distinct histotypes with differing cells of origin and risk factor profiles, any diabetes-related signal may vary across subtypes. These considerations suggest that small average associations in aggregate data could conceal sharper effects in particular contexts defined by metabolic milieu, reproductive history, or tumor histology. Several determinants, including adiposity, age, and hormonal exposures, are shared between diabetes mellitus and ovarian cancer, which further complicates the separation of their independent effects [ 10 ]. Higher circulating glucose and insulin concentrations, chronic low-grade inflammation, plus oxidative stress have been proposed as overlapping mechanisms which might promote cellular proliferation, impair apoptosis, and increase DNA damage; thereby facilitating carcinogenesis [ 11 – 13 ]. Additionally, antidiabetic medications may differentially modulate the risk regarding cancer; insulin and some insulin secretagogues are suggested to be able to amplify mitogenic signaling, whereas metformin has been hypothesized to exert anticancer effects through activation of AMP-activated protein kinase plus inhibition of mTOR signaling; despite current evidence remaining inconclusive [ 14 – 18 ]. Epidemiologic findings to date have been mixed. Several cohort and case–control studies have reported small positive associations between DM and incident OC, whereas others have observed null or imprecise estimates [ 19 – 23 ]. Earlier syntheses reached broadly similar conclusions while noting substantial heterogeneity attributable to differences in population characteristics, exposure and outcome ascertainment, and confounder adjustment [ 19 , 24 ]. In parallel, evolving OC classification and limited histotype-resolved reporting complicate interpretation of legacy datasets, and granularity on DM phenotype, duration, glycemic control, and treatment exposure has often been insufficient for stratified analyses. The present study was undertaken to provide an updated, PRISMA-guided systematic review and meta-analysis of observational studies evaluating the association between DM and incident OC. The protocol was prospectively registered and standard methods were used for study identification, selection, data extraction, and quality assessment [ 25 – 27 ]. By consolidating the contemporary literature with transparent methodology and predefined effect modifiers, this analysis aims to provide an up-to-date pooled estimate of the association between DM and OC and to identify where residual gaps—such as limited histotype resolution and heterogeneous exposure and outcome definitions—continue to constrain inference. Given the relatively low incidence of OC, any population impact of a diabetes-related signal is expected to be modest; consequently, results are interpreted with attention to both relative and absolute scales, and with emphasis on research priorities that can sharpen causal interpretation and clinical relevance.

Supplementary Material 1 Supplementary Material 1