A Systematic Review and Meta-analysis of Associations between Clinical Prostatitis and Prostate Cancer: New Estimates Accounting for Detection Bias

As many as 20% of all cancers, including those of the colon, liver, stomach, esophagus, and pancreas, are estimated to be caused, at least in part, by chronic inflammation and inflammatory diseases (1, 2). Chronic inflammatory processes have also been hypothesized to contribute to the development of other cancers, such as prostate cancer (3, 4). One key piece of evidence supporting this hypothesis is findings from epidemiologic studies of clinical prostatitis (ostensibly “prostate inflammation”) and prostate cancer. Overall, meta-analyses of these studies have observed strong positive associations between clinical prostatitis and prostate cancer, supporting a role for prostate inflammation in prostate cancer development (5–8). However, none of these meta-analyses took into consideration the potential for detection bias in their pooled estimates. This bias may occur if men with clinical prostatitis are more likely to be screened or investigated for prostate cancer than men without prostatitis. For instance, men with clinical prostatitis may be more likely to be screened for prostate cancer than men without symptoms to rule prostate cancer out as a cause of their symptoms or because of continued visits to a urologist following their prostatitis diagnosis. Clinical prostatitis may also cause men's prostate-specific antigen (PSA) levels to rise (9), possibly contributing to an increased likelihood of prostate biopsy and occult prostate cancer detection. Although many of these possibilities have been recognized by previous authors and addressed in a few individual studies, none of the systematic reviews and meta-analyses performed to date have taken this bias into consideration.

To address this concern, we performed an updated systematic review and meta-analysis of associations between clinical prostatitis and prostate cancer, accounting for detection bias. Our updated meta-analysis also addressed additional methodological issues identified in previous meta-analyses, such as inclusion of duplicate studies (6–8), inclusion of estimates for exposures similar in spelling to, but distinct from, “prostatitis” (i.e., “prostitutes”; refs. 6, 7), and exclusion of cohort studies (7).

This study was completed in accordance with guidelines for the conduct of systematic reviews and meta-analyses of observational studies, as well as the PRISMA statement (10, 11). All observational studies (cohort, nested case–control, case–control, and cross-sectional) investigating the association between clinical prostatitis and prostate cancer in humans were eligible. Studies with an exclusive focus on asymptomatic inflammation (NIH category IV prostatitis; ref. 12) in biopsy or radical prostatectomy specimens were not included.

The published literature was searched from January 1, 1946, to November 30, 2018, without language restrictions, using strategies created by a medical librarian. Search strategies were established and implemented in Ovid Medline, Embase, Scopus, Cochrane Central Register of Controlled Trials, Database of Abstracts of Reviews of Effects, Cochrane Database of Systematic Reviews, Clinicaltrials.gov, and WHO International Clinical Trials Registry Platform. Standardized terms and key words were used, including prostatitis, prostatic inflammation, prostatic neoplasms, and prostate cancer (Supplementary Methods and Materials). The titles and abstracts of 2,306 articles were screened to exclude reviews, case reports, commentaries or editorials, abstracts only, animal studies, and original articles without usable effect estimates (Supplementary Fig. S1). Following abstract review, a manual search was conducted for references cited in selected articles or previous reviews on this topic. In addition, the full text of articles examining genitourinary conditions (e.g., urethral stricture, cystitis, sexually transmitted infections) or procedures (e.g., vasectomy) in relation to prostate cancer were searched for prostatitis effect estimates because many older studies that investigated clinical prostatitis as part of a larger number of possible risk factors—typically other genitourinary conditions or procedures—did not always include references to clinical prostatitis in their abstract. When multiple articles from the same study population were found, the most recent or complete publication was included. One exception was two studies performed among health plan members at Kaiser Permanente (13, 14). Although these studies overlapped by some years of enrollment, we retained both studies because of their likely minimal overlap in study participants as Weinmann and colleagues only included fatal prostate cancer cases. Two independent reviewers performed the literature review with disagreement settled by a third independent reviewer.

Data extraction was completed by two of three independent reviewers. Inconsistencies were rereviewed by another independent reviewer and disagreement resolved by consensus among all reviewers. Any necessary information not found in the articles was obtained by contacting the corresponding author. Foreign articles were translated by reviewers with native language experience. When multiple estimates were reported in a study, we chose the most fully adjusted estimate. For studies reporting estimates from multiple control groups, we report only estimates derived from population-based and non-cancer hospital controls if possible (15–17). However, studies that did not separate non-cancer from cancer controls were retained (18–20). We assessed the quality of each study using a revised classification system based on the Newcastle-Ottawa Quality Assessment Scale (21). This score ranged from 0 to 8 and included items for (i) type of controls [i.e., population-based, hospital-based, or with benign prostatic hyperplasia (BPH)]; (ii) characterization of cases (e.g., incident and histologically confirmed); (iii) similarity of response rates between cases and controls; and (iv) method of clinical prostatitis assessment (i.e., self-report or medical record based).

To address detection bias, we identified all studies that accounted for this bias, and reviewed their methods to develop three distinct groups of detection bias methods. These groups were developed without regard to the point estimates of each study and included in order of decreasing methodologic rigor (i.e., from most to least methodologic rigor): (i) Exclusion of prostatitis diagnoses in the short window before prostate cancer detection to reduce the possible influence of recent prostatitis diagnoses or symptoms on incidental prostate cancer detection. Studies within this category provided estimates excluding participants whose prostatitis diagnosis occurred less than 1, 2, or 5 years before prostate cancer diagnosis for cases or before the index date for controls. (ii) Stratification/restriction based on prostate cancer screening to reduce the possible influence of a greater likelihood of routine prostate cancer screening among men diagnosed with prostatitis. Here, studies provided stratified or restricted estimates based on any recent PSA or digital rectal examination (DRE) screening for prostate cancer (1–2 years prior to diagnosis), any lifetime PSA or DRE screening for prostate cancer, number of recent PSA tests, or selection of study populations likely to engage in enhanced prostate cancer screening (i.e., men with BPH, men in the intervention arm of the Prostate, Lung, Colorectal, and Ovarian Cancer Screening Trial). (iii) Adjustment based on prostate cancer screening. Studies within this category adjusted statistical models for any of the previously mentioned screening methods or the frequency of physician visits. These three groups were compared with studies that did not take detection bias into account. Ideally, we would have also created a category for studies that met the criteria for both methods (i) and (ii), but too few studies met the criteria for both of these methods to allow for separate analyses. Finally, we performed sensitivity analyses combining studies that used either method (i) or method (ii), recognizing that these methods could possibly be ranked interchangeably; and analyses combining all three methods.

We calculated summary odds ratios (OR) to describe the association between clinical prostatitis and prostate cancer overall and within strata defined by detection bias methods. For our overall estimate, we performed the analysis in two different ways. First, we selected one estimate per study (typically the most adjusted estimate presented in either the abstract, main table, or conclusion of the manuscript, or in a previous meta-analysis using population-based controls when possible) and pooled these estimates using a traditional random effects model (22, 23). This pooled OR was calculated for comparison with previous meta-analysis results, and heterogeneity was evaluated using the I² statistic. For our second method, we included all maximally adjusted estimates from each detection bias stratum per study and used a random effects model with robust variance estimation to account for inclusion of multiple estimates per study (24–26). A separate heterogeneity statistic was not calculated for this overall estimate because robust variance estimation incorporates between-study heterogeneity into pooled estimates and is robust to misspecification of the underlying covariance structure (24).

To address detection bias, we calculated separate pooled estimates within strata defined by detection bias methods. To evaluate the incremental influence of detection bias methods on the summary point estimates, we assigned a score based on the rigor of each method and modeled as a linear function in the meta-regression model (i.e., a test for linear trend; ref. 27). We also performed several subgroup and sensitivity analyses to assess the possible influence of other factors on our summary estimates. These included: (i) analyses stratified by study design; type of controls; prostatitis assessment method; study location and participant race/ethnicity; study quality; and age at prostate cancer diagnosis; (ii) analyses restricted to studies assessing “chronic” prostatitis, as chronic exposures are typically more likely to contribute to cancer than to acute exposures (8); (iii) analyses excluding studies with control selection based on the presence or absence of benign prostatic conditions including BPH; (iv) analyses limited to aggressive prostate cancer (SEER grades III–IV, or Gleason grade ≥7); and (v) analyses taking into consideration prostatitis treatment or regular anti-inflammatory drug use. Each of these analyses accounted for detection bias methodology used (any vs. none). Finally, to examine the influence of potentially unpublished studies on the summary OR estimates, funnel plots were created by regressing the log OR on the sample size and weighting by the inverse pooled variance (28). All analyses were performed in STATA version 15.

A total of 38 studies were selected for inclusion in the final meta-analysis (Table 1). Of these studies, 10 were prospective (3 cohort and 7 nested case–control), 26 were case–control (14 population-based, 6 hospital-based, 3 population and hospital-based, 2 family-based, and 1 BPH-based controls), and 2 were cross-sectional. Studies were derived from diverse populations in North America (n = 24), Europe (n = 3), Australia (n = 1), the Middle East (n = 2), and Asia (n = 8). Ten included populations comprising at least 20% men of African descent (African American men and men of African descent from Barbados). Sample sizes for included studies ranged from 124 to 35,586 participants.

When estimates from all studies were combined irrespective of the potential influence of detection bias, a significant positive association was observed between clinical prostatitis and prostate cancer, using both a “main estimate” approach [OR, 2.10; 95% confidence interval (CI), 1.69–2.61; I² = 91.1, P ≤ 0.001; Fig. 1A], as well as an approach accounting for all 51 reported study estimates (OR, 2.05; 95% CI, 1.64–2.57; Fig. 1B). As these approaches produced estimates very similar in magnitude, we performed all further analyses using all available estimates per study.

Next, we conducted stratified analyses by detection bias methodology to evaluate the potential influence of detection bias on our pooled estimate (Table 2). Among studies that did not use methods to address detection bias, a strong positive association was observed (OR, 2.75; 95% CI, 2.09–3.61) of even greater magnitude than our overall pooled estimate. However, in all other strata of studies that addressed detection bias, attenuated, nonsignificant associations were observed, with increasingly greater attenuation as the rigor of detection bias methodology improved (P = 0.0002). Specifically, among studies that adjusted for prostate cancer screening or markers of screening, the least rigorous method for addressing detection bias, a weaker, nonsignificant, but still suggestive, positive association was observed (OR, 2.08; 95% CI, 0.97–4.47). This association weakened among studies that provided estimates restricted to screened men (OR, 1.36; 95% CI, 0.93–1.99) and weakened even further to the null among studies that excluded prostatitis diagnoses in the short window before prostate cancer diagnosis, the strongest method for addressing detection bias (OR, 1.16; 95% CI, 0.77–1.74). Although the sample sizes for some subgroup analyses were small, even combining the two most rigorous categories (OR, 1.26; 95% CI: 0.90–1.77) or grouping by any method of addressing detection bias resulted in nonsignificant, attenuated associations (OR, 1.45; 95% CI, 0.98–2.15).

To explore additional factors that might explain some of the variation across study findings, we performed further stratified analyses, taking into account detection bias to the degree possible (any vs. no method). Although no significant differences were observed across strata defined by study methodology, nonsignificantly weaker associations were observed in studies less susceptible to recall bias (i.e., prospective studies, those that assessed prostatitis by medical record review, and higher quality studies), possibly suggesting a role for recall bias in explaining our overall findings (Table 3). To explore this possibility further, we adjusted our detection bias–stratified results by susceptibility to recall bias and observed a slight attenuation of the estimates (OR, 2.01; 95% CI, 1.51–2.68 among studies that did not account for detection bias and OR, 1.19; 95% CI, 0.78–1.82 among studies that used any method to reduce detection bias; Table 2), suggesting an additional small influence of recall bias on previous prostatitis and prostate cancer findings.

In analyses stratified by geography and race/ethnicity, we observed a stronger positive association among men of African descent (OR, 1.73; 95% CI, 0.90–3.33; Table 3) than among those of European descent (OR, 1.38; 95% CI, 1.05–1.80), even after accounting for detection bias. Some evidence of a stronger positive association was also seen among Asian American men (OR, 2.23) and men residing in East Asia (OR, 2.45; 95% CI, 1.37–4.37) and the Middle East (Iran and Jordan; OR, 6.17), although the precision of several of these summary ORs was unreliable due to the limited number of estimates in each group. With respect to age at prostate cancer diagnosis, only two studies explored the association of clinical prostatitis and prostate cancer stratified by age and accounting for detection bias (29, 30). Sutcliffe and colleagues (29) observed a significant positive association between clinical prostatitis and prostate cancer among younger men (<59 years) screened for prostate cancer (OR, 1.49; 95% CI, 1.08–2.06). However, this association was null among those ages 59 to 68 years and became protective among older men (≥69 years; OR, 0.79; 95% CI, 0.64–0.98). Similarly, Zhu and colleagues (30) found evidence of a positive association among younger men (40–64 years; OR, 1.78; 95% CI, 0.82–3.85) that attenuated among older men (65–69 years; OR, 1.24; 95% CI, 0.67–2.29).

With respect to prostatitis type, null associations were observed among studies defining their exposure as chronic prostatitis, whereas positive associations (OR, 1.66; 95% CI, 1.26–2.18) were observed when prostatitis subtype was not further specified. No differences in findings were observed between U.S. studies conducted prior to 1987, the period before widespread PSA testing, and those conducted from 1987 onward. In analyses limited to aggressive prostate cancer, some evidence of a null association was seen (OR, 1.03), although small sample sizes rendered this estimate unreliable. Null associations were also found in studies investigating advanced stage (T_3b or worse; OR, 0.81; 95% CI, 0.50–1.30; ref. 29) and fatal prostate cancer (OR, 1.0; 95% CI, 0.79–1.4; ref. 14)). No appreciable differences were observed in the overall pooled estimate when we excluded studies that either enriched (31, 32) or depleted (13, 15, 16, 18, 20, 33–35) their control populations of prostate conditions (e.g., BPH, high PSA, all benign prostate conditions). In the sole study using BPH controls, Checkoway and colleagues (31) found some evidence of an inverse association (OR, 0.38; 95% CI, 0.01–4.11). Finally, with respect to prostatitis treatment, only two studies assessed the possible influence of treatment or management of prostatitis either directly (29) or indirectly (36) on the association between clinical prostatitis and prostate cancer. Sutcliffe and colleagues (29) found similar null results among those treated (RR, 0.95; 95% CI, 0.83–1.09) and not treated (RR, 1.10; 95% CI, 0.65–1.84) for prostatitis, whereas Doat and colleagues (36) found that nonsteroidal anti‐inflammatory drug (NSAID) use modified the association of prostatitis and prostate cancer, with a potentially positive association among non-NSAID users (OR, 2.11; 95% CI, 1.29–3.43) and a null association among ever users (OR, 0.83; 95% CI, 0.44–1.58).

To evaluate the impact of publication bias on our meta-analysis conclusions, we used Begg funnel plot and statistical test, as well as Egger test. Visual inspection of Begg funnel plots suggested some funnel asymmetry (Fig. 2), but statistical tests indicated a lack of significant publication bias (Begg test z = 0.82, P = 0.414; Egger test t = 1.39, P = 0.175).

In our systematic review and meta-analysis of 38 studies, we found that a history of clinical prostatitis was statistically associated with prostate cancer, but only when pooled estimates did not account for detection bias. When estimates did take detection bias into account, the overall pooled association was considerably weaker and nonsignificant, with a significant inverse linear trend between the degree of a priori–defined detection bias methodologic rigor and the strength of the observed association. Specifically, the association decreased from an approximate 2-fold increased odds of prostate cancer in the stratum that did not address detection bias down to a null association in the stratum that used the most rigorous method to reduce detection bias. Although the sample size for this last analysis was small, inferences from this stratum are supported by the strong linear trend between the degree of detection bias methodologic rigor and the magnitude of the association, as well as the nonsignificant overall pooled association among studies that used any method to reduce detection bias, regardless of the chosen method. Furthermore, our stratified findings suggest that much of the previously observed positive associations between clinical prostatitis and prostate cancer may have been driven by recent prostatitis diagnoses, prompting increased prostate cancer screening and/or investigation.

To our knowledge, we are the first to examine the influence of detection bias on the pooled association between clinical prostatitis and prostate cancer, precluding a comparison of our detection bias findings to previous meta-analyses. However, our overall findings not taking detection bias into consideration are similar in direction and magnitude, if not stronger, than those from previous meta-analyses (1.57, 95% CI, 1.01–2.45, ref. 5; 1.64, 95% CI, 1.36–1.98, ref. 7; and 1.68, 95% CI, 1.57–1.79, ref. 6), suggesting that similar results would have been observed in these meta-analyses had they taken detection bias into consideration and that our findings are not driven by differing eligibility criteria or inclusion of more recent studies. Likewise, our additional stratified findings are also consistent with those from previous meta-analyses. These include findings from analyses stratified by type of controls (5, 6) and method of prostatitis assessment (6, 7), many of which were lower in magnitude in studies that ascertained prostatitis exposure by medical record review. Together with our lower pooled estimates in prospective studies and those with higher methodologic quality, these findings support a possible role for differential recall bias—i.e., the probability that cases may have been more likely to recall or report a diagnosis of prostatitis than controls—in explaining some of our overall findings. Indeed, when we adjusted our detection bias stratified findings for susceptibility to recall bias, our pooled estimates attenuated even further. Nevertheless, this attenuation was considerably less than that observed after accounting for detection bias, suggesting that detection bias was the major contributor to previously observed positive findings.

Findings stratified by geography and race/ethnicity were also consistent with those from previous meta-analyses (6–8). Notably, our estimate for men of African descent was stronger than observed among Caucasian men, possibly because of lower background rates of prostate cancer screening in unexposed men (i.e., those without a history of prostatitis), giving exposed men a greater screening advantage and likelihood of prostate cancer detection. We also observed a stronger association among East Asian and Asian American men, the latter of which we believe is the first such mention in the literature. Reasons for these stronger associations are unclear, but could include (i) a similar screening advantage as described above for men of African descent, although the lower background rates of screening in this group would likely be driven by lower disease risk rather than lesser screening access; and (ii) historical patient counseling patterns in some Asian countries in which prostate cancer patients were informed they had benign prostate conditions, such as prostatitis, rather than prostate cancer to avoid alarming them (37), a practice that may have been continued following migration. However, given the small number of studies conducted in Asian American populations, additional studies are needed before any conclusions can be drawn about the magnitude of their association and its meaning. Similarly, the vast heterogeneity in estimates from the Middle Eastern studies precludes any conclusion based on their pooled estimate. Finally, in terms of tumor aggressiveness, only three studies provided estimates for aggressive prostate cancer (29, 38, 39), reducing the reliability of the standard error of the pooled estimate. However, the lower magnitude of this pooled estimate is consistent with our conclusion that previous findings were influenced by detection bias, as aggressive prostate tumors should be less susceptible to detection bias than nonaggressive tumors that may never have been diagnosed without prostate cancer screening or investigation (38).

Although our overall conclusion is that previous positive findings between clinical prostatitis and prostate cancer were driven by detection bias, we do not believe this conclusion rules out a role for prostate inflammation in prostate carcinogenesis because of the nature of the conditions captured by “clinical prostatitis.” This diagnosis represents a heterogeneous group of conditions, including acute bacterial prostatitis (NIH category I prostatitis), chronic bacterial prostatitis (category II), inflammatory chronic prostatitis/chronic pelvic pain syndrome (CP/CPPS, category IIIa), and noninflammatory CP/CPPS (category IIIb; ref. 12), the latter of which may account for up to 45% of all prostatitis diagnoses (12, 40). Therefore, clinical prostatitis broadly may not accurately reflect prostate inflammation or address our original hypothesis. Although we saw a null association among studies assessing chronic prostatitis broadly (OR, 0.84; 95% CI, 0.52–1.36), only two studies to date have distinguished clinical prostatitis subtypes more likely to reflect prostate inflammation, both of which accounted for detection bias and used diagnoses confirmed by laboratory evidence of infection/inflammation. The first of these studies observed positive associations for acute (OR, 1.9; 95% CI, 0.9–3.8) and chronic bacterial prostatitis (OR, 1.6; 95% CI, 0.8–3.1), but not for chronic nonbacterial prostatitis (OR, 0.9; 95% CI, 0.4–1.8; ref. 41), and the second observed generally null associations for acute (OR, 0.92; 95% CI, 0.51–1.67) and chronic (OR, 0.79; 95% CI, 0.53–1.17) bacterial prostatitis (32). These conflicting results highlight the importance of additional work in this area focused specifically on chronic bacterial prostatitis and inflammatory CP/CPPS, and accounting for detection bias.

Besides bacterial prostatitis and inflammatory CP/CPPS, inflammation may also be present in the prostate asymptomatically (NIH category IV prostatitis; ref. 12), a condition that was not studied in the present meta-analysis. Agreement between this common condition (42) and clinical prostatitis has been found to be low (e.g., 47.8%; refs. 32, 43), possibly suggesting distinct conditions. Interestingly, in a meta-analysis of 25 studies of asymptomatic prostatitis diagnosed based on thin needle biopsy, men with histologic prostate inflammation had a 55% overall decreased (rather than increased) odds of prostate cancer compared with those with no evidence of inflammation (44). This unexpected finding may be explained by several possible reasons. First, inflammatory cells (macrophages and lymphocytes) may potentially protect against prostate cancer by destroying “foreign” malignant cells (i.e., immunosurveillance) and preventing them from developing into a prostate tumor (45). Second, the study design/eligibility criteria of included studies may have led to a spurious protective association. Histologic studies depend on available prostate biopsy tissue for all participants, which typically requires a clinical indication for biopsy, such as an elevated PSA concentration. However, because PSA may rise for reasons other than prostate cancer, such as prostate inflammation, it is possible that previous studies may have observed a seemingly protective association because participants' PSA was elevated for one, but not the other, reason—i.e., in the simplest scenario, if participants' PSA was elevated because of prostate inflammation, then it was not elevated because of prostate cancer, leading to a protective association. Therefore, a better population in which to study asymptomatic prostatitis and prostate cancer may be men with prostate tissue available, but who were unselected for clinical indication for biopsy. One such unique study population with both of these features is the Prostate Cancer Prevention Trial (PCPT). In this study, the authors observed a positive association between asymptomatic inflammation and total and high-grade prostate cancer (OR, 1.78; 95% CI, 1.04–3.06 and OR, 2.24; 95% CI, 1.06–4.71, respectively; ref. 46) that persisted when restricted to those with low PSA concentration (<2 ng/mL) and those without a clinical indication for biopsy. Further prospective evidence of this association was observed among PCPT participants who had not developed cancer by the conclusion of the original study, but who were followed subsequently for prostate cancer (OR, 1.66; 95% CI, 0.70–3.96; ref. 47). Alternative study populations in which to investigate this challenging question include historical cohorts of BPH patients who underwent transurethral resection of the prostate and who were subsequently followed for prostate cancer incidence and mortality (48).

This meta-analysis represents the most expansive to date and the first to evaluate the association between clinical prostatitis and prostate cancer accounting for detection bias. However, in addition to the heterogeneity of diagnoses captured by “clinical prostatitis,” our meta-analysis has several further limitations. First, only eight studies to date have performed analyses excluding recent prostatitis diagnoses, reducing the precision of our least-biased pooled estimate, and even fewer have performed analyses excluding recent prostatitis diagnoses and stratifying by prostate cancer screening. Nonetheless, although more studies are certainly warranted, our findings are still supported by the nonsignificant association observed when any method to reduce detection bias was used, and the highly significant inverse trend between the degree of methodologic rigor for addressing detection bias and the magnitude of the observed association. Second, we were not able to account for increased prostate cancer detection because of incidental prostate cancer diagnosis on biopsies triggered by prostatitis-mediated PSA elevation. However, residual detection bias would only be expected to attenuate our null results further. Third, we were unable to fully explore differences in the magnitude of association between subgroups of interest (e.g., aggressive prostate cancer) independent of detection bias because of the small number of studies that addressed detection bias within these subgroups. Small numbers also limited our meta-regression adjustment to “any” versus “no” method to reduce detection bias. Finally, we were not able to investigate possible differences in the association between clinical prostatitis and prostate cancer by age at prostate cancer diagnosis or a possible protective influence of therapy (e.g., antibiotics) or anti-inflammatory medications (e.g., NSAIDs) on this association because of the small number of studies that performed these types of analyses (29, 30, 36).

Overall, our findings indicate that previously reported associations between clinical prostatitis and prostate cancer were likely the result of detection bias. Additionally, even in the absence of detection bias, “clinical prostatitis” not further specified may not be an appropriate proxy for prostate inflammation. Future studies should address these concerns by focusing on inflammation-related types of clinical prostatitis (confirmed acute and chronic bacterial prostatitis, and inflammatory CP/CPPS), collecting detailed exposure data (e.g., age at onset, treatment, etc.) prospectively, and accounting for detection bias. Ultimately, some association between prostate inflammation and prostate cancer is biologically plausible; however, most epidemiologic studies conducted to date have not demonstrated this relation without serious concerns for bias. Correctly estimating this possible relation is important not only for etiologic purposes, but also for reassuring or properly counseling and screening men with prostatitis about their future risks of prostate cancer, given their documented concerns for developing this malignancy (49–51).

No potential conflicts of interest were disclosed.

This work was supported by the Barnes-Jewish Hospital Foundation and Alvin J. Siteman Cancer Center. M.E. Langston was additionally supported by the NCI of the NIH under award number T32CA190194. S. Khan was additionally supported by DOD Prostate Cancer Research Program grant PC170173. The content of this work is solely the responsibility of the authors and does not necessarily represent the official views of the NIH.

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