a tumor that would otherwise remain obscure during lifetime manifests itself clinically. In case 4, no contribution of exposure is pos- sible. Unfortunately, little is known about the duration of these phases. Furthermore, there are likely gross differences between tumor types concerning absolute and relative length of these steps during natural history of the disease. Although slowly growing tumors such as most meningioma and schwannoma may have unchanged growth rates during pro- longed periods of time, other brain tumors such as glioblastoma show an explosive final growth after possibly long periods of more stable behavior. For radiation-induced tumors, Cahan et al. (1948) proposed to allow at least 5 years for induction periods. As delineated above, for an effect during latent growth to be detected in epidemiologic studies, exposure must have been during a substantial propor- tion of growth phase. Therefore, for an influ- ence both during the induction phase and on tumor growth rate, at least 5 years must be allowed for latency or duration of exposure, respectively, to fulfill the criterion of temporal relation. Because for virtually all carcinogens, repetitive or prolonged exposures are necessary to bring about an increased cancer incidence, it is necessary to consider not only time since first exposure but also duration of exposure. Number of calls and average duration of calls seem to be too difficult to remember for peri- ods far in the past, but information about peri- ods of regular use is more easily recalled and therefore could be the best choice for exposure determination. (In principle, it may even be validated by network provider data). Years of regular mobile or cordless phone use up to 5 years before diagnosis would possibly be the appropriate exposure meter for most slowly growing tumors. Because such evaluations have not been performed, I instead assessed exposure duration or latency of ≥ 10 years, as available, for Table 1. In these subjects, at least half of the exposure duration falls within an etiologically relevant period. Association. I computed a meta-analyti- cal estimate of the risk for the different brain tumor types based on all independent studies reporting ORs for ≥ 10 years of mobile phone use. Heterogeneity was assessed by chi-square tests. A p-value < 0.05 was considered signifi- cant. If studies included the same population, only those without overlap were considered in the meta-analyses. Pooled effects and SEs were derived from the fixed-effect model because no significant heterogeneity was detected. Because basically all investigations used the same study design and the same end point definition, despite some deviations in exposure classifica- tion and proneness to misclassification and selection bias, no attempt was made in the meta-analysis to account for these differences. It should, however, be noted that correction for selection and misclassification bias would lead to higher meta-analytical odds ratios. There is no publication bias in this case because all stud- ies that are planned, ongoing, or completed are known to the scientific community. For glioma, I included three studies (Hardell et al. 2006c; Lahkola et al. 2007; Schüz et al. 2006a) reporting data on 233 exposed cases and 330 exposed controls among 2,792 glioma patients and 6,195 control subjects. I found no heterogeneity across studies, and the com- bined OR was 1.5 [95% confidence interval (CI), 1.2–1.8]. For acoustic neuroma, two independent pooled analyses (Hardell et al. 2006b; Schoemaker et al. 2005) gave an over- all OR of 1.3 (95% CI, 0.95–1.9), based on 67 exposed cases and 311 exposed controls among 912 and 5,715 cases of acoustic neu- roma and controls, respectively. Risk for men- ingioma from mobile phone use of ≥ 10 years was reported in two individual studies (Hardell et al. 2006b; Schüz et al. 2006a) and one pooled study (Lahkola et al. 2008), with an overall OR of 1.1 (95% CI, 0.8–1.4) evalu- ated from 116 exposed cases and 320 controls among a total of 2,506 meningioma patients and 6,223 control subjects. Hence, there is an increased risk for all of these end points from mobile phone use that is statistically significant for glioma. In these analyses mobile phone use was assumed to induce the neoplasia. If mobile phone use has an additional or exclusive effect on tumor growth, this analysis is not entirely appropriate because an effect on the grow- ing tumor can only be exerted by exposure on the same side of the head where the tumor is located. Combined estimates for ipsilateral mobile phone use of ≥ 10 years give the ORs: 1.9 (95% CI, 1.4–2.4) for glioma; 1.6 (95% CI, 1.1–2.5) for acoustic neuroma; and 1.3 (95% CI, 0.9–1.9) for meningioma. Hence, there are clear indications of increased risks for all three end points. According to the dialogue approach, association must be assessed whether or not there are valid counterarguments, and espe- cially those based on considerations about the impact of possible biases. Potential biases. As apparent from Table 1, ever (regular) use of a mobile phone rarely revealed increased risks for any type of brain tumor. Except for the Finnish study of Auvinen et al. (2002), only the Swedish group of Hardell and colleagues (e.g., Hardell et al. 2002a) reported significantly elevated estimates of relative risks. Most studies summarized in Table 1 were conducted based on the Interphone protocol (Cardis et al. 2007) that defined regular use as at least one outgoing or incoming call per week for at least 6 months, with ever-regular use start- ing 1 year before the reference date. Although the reference date was defined as date of diag- nosis in cases and the same date of the matched Environmental Health Perspectives • volume 117 | number 3 | March 2009 Mobile phones and cancer control, in studies not individually matched (e.g., Hepworth et al. 2006), there are problems in defining the reference date because of the interview lag time. Because of the rapid increase in mobile phone use during and before the study period, the methods applied to compute the reference date for controls could be a source of bias. Information provided in the study reports is insufficient to decide whether adjust- ments were biased. In some articles (Hepworth et al. 2006; Schoemaker et al. 2005), controls were allocated into categories of interview lag time at random without consideration of age and sex of the cases within these categories, whereas in others (Lönn et al. 2004a), aver- age lag between diagnosis and identification in a matched set was subtracted from date of control identification. The first method intro- duces bias if distribution of age and sex within categories of lag times differs, and the second method introduces bias if the date of identifi- cation differs between cases and controls. To my knowledge, these possible biases have not been considered previously. In the Interphone study (Cardis et al. 2007), data were collected from the end of 2000 through the beginning of 2004, with some differences between countries. During this period, mobile phone penetra- tion rate increased from about 60% to about 90% in the European Union, according to the International Telecommunication Union. Insufficient adjustment for differences in the interview date would result in underestimation of risk. In their studies, Hardell and colleagues disregarded mobile and cordless phone use within the last year before the reference date. Any use of a mobile or cordless phone was counted except when hands-free devices or external car antennas were used. The reference date for controls was set to the date of diag- nosis of the matched case. In some reports of pooled data sets (e.g., Hardell et al. 2006c), individual matching was disregarded and con- trols from different studies were included. Insufficient adjustment of the reference date could have also led to bias in this case. Hardell and colleagues defined the unex- posed subjects as those who have not used a mobile or cordless phone for ≥ 1 year before diagnosis (or reference date in controls). The Interphone group disregarded cordless phones in analyses of mobile phone use (and vice versa). Cardis et al. (2007) and Takebayashi et al. (2006) have argued that cordless phone use is associated with much lower exposure to microwaves and therefore cannot be counted in exposure assessments. This view is not cor- rect. Average power levels are not much dif- ferent between cordless phones (average levels of 10 mW) and mobile phones (median aver- age output power 6–16 mW in urban areas) (Lönn et al. 2004b). Considering the typi- cally longer duration of daily use of cordless 319