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Describing the relatedness between study units is critical to capture features of pedigree studies involving heritability, including power and precision of heritability estimates. Blangero et al. (Adv Genet 81:1–31, ) showed that in pedigree studies the power to detect heritability is a function of the true heritability and the eigenvalues of the kinship matrix. We extend this to a more general setting which allows statements about expected precision of heritability estimates. Using two different Taylor series approximations, we summarize the relatedness in a study design by one or two parameters. These relatedness summary parameters (RSPs) are functions of the eigenvalues or log-eigenvalues of the kinship matrix. Using the RSPs based on the log-eigenvalues, we accurately approximate the expectation of the likelihood ratio test and expected confidence interval widths. We define an effective sample size of a target study as one which has the equivalent power and precision to a reference design. Using unrelated sibpairs as the reference design provides very accurate assessments of power. RSPs and effective sample sizes provide new tools for comparing studies and communicating information about relatedness in heritability studies. Acknowledgments We would like to thank the Genetic Analysis Workshop (GAW) 13 organizers for allowing us to use the simulated pedigree data in this paper. We also thank Dr. Ellen Wijsman for permitting us to use the Guam pedigree structure, as well as the two anonymous referees who provided insightful comments to our paper. This research was supported in part by the National Institutes of Health grants GM046255 and GM099568 and a Pacific Institute for the Mathematical Sciences postdoctoral fellowship. ![]() ![]() ![]() Methods and Findings For 14,886 meta-analyses of binary outcomes from 1,991 Cochrane reviews, we calculated power per study within each meta-analysis. We defined adequate power as ≥50% power to detect a 30% relative risk reduction. In a subset of 1,107 meta-analyses including 5 or more studies with at least two adequately powered and at least one underpowered, results were compared with and without underpowered studies. In 10,492 (70%) of 14,886 meta-analyses, all included studies were underpowered; only 2,588 (17%) included at least two adequately powered studies. 34% of the meta-analyses themselves were adequately powered. The median of summary relative risks was 0.75 across all meta-analyses (inter-quartile range 0.55 to 0.89). In the subset examined, odds ratios in underpowered studies were 15% lower (95% CI 11% to 18%, P. In the United States, Studysize.com is ranked 4,353,113, with an estimated 430 monthly visitors a month. Click to view other data about this site. Easy-to-use software for the calculation and analysis of the statistical power, sample size or any other parameter in a study design. Includes tests, point estimates. StudySize (StudySize3.0Trial.exe). StudySize is a user friendly program for sample size and power calculations when planning a study, clinical trial, survey,. Citation: Turner RM, Bird SM, Higgins JPT (2013) The Impact of Study Size on Meta-analyses: Examination of Underpowered Studies in Cochrane Reviews. PLoS ONE 8(3): e59202. Editor: Lise Lotte Gluud, Copenhagen University Hospital Gentofte, Denmark Received: November 15, 2012; Accepted: February 14, 2013; Published: March 27, 2013 Copyright: © 2013 Turner et al. This is an open-access article distributed under the terms of the Creative Commons Attribution License, which permits unrestricted use, distribution, and reproduction in any medium, provided the original author and source are credited. Funding: This work was funded by Medical Research Council grants U105285807 and U105260794. The funders had no role in study design, data collection and analysis, decision to publish, or preparation of the manuscript. Competing interests: RMT and JPTH declare that no competing interests exist. The authors have the following interest. SMB holds Glaxo shares. This does not alter the authors' adherence to all the PLOS ONE policies on sharing data and materials, as detailed online in the guide for authors. Introduction Systematic reviews of intervention studies aim to synthesise all available evidence meeting pre-specified eligibility criteria. Such criteria seldom address sample size. Meta-analyses may therefore include data from one or more small studies which, individually, do not have power to detect a modest intervention effect. Small studies tend to report greater intervention effects than larger studies. So-called “small-study effects” may arise from reporting biases, whereby findings in smaller studies are more likely to be selected for publication on the basis of statistical significance. Alternatively, small-study effects may arise from biases caused by methodological flaws arising more frequently in small studies, or may be due to true differences in the underlying effects between smaller and larger studies. Some researchers argue for excluding small studies from meta-analyses. Specifically to reduce the effects of publication bias, Stanley suggested discarding 90% of the study estimates, so that conclusions are based on only the most precise 10% of studies. Earlier, Kraemer proposed including only adequately powered studies in meta-analysis, both to remove publication bias and to discourage future researchers from carrying out small studies. In teaching, Bird has long advocated that trials should not be started unless they could deliver at least 50% power in respect of a priori plausible, worthwhile effect sizes. The prospect of inclusion in later meta-analyses may partly explain why investigators continue to feel justified in conducting underpowered studies –. Researchers who choose to undertake a study that is capable of detecting only an unrealistically large effect may lack understanding of both scientific methods and ethics. Arguments for including small studies in meta-analyses uphold that evidence synthesis is best informed by all reasonably unbiased evidence and that no such evidence should be discarded lightly. Cut-offs based on study size, although scientifically cost-efficient, introduce an extra element of subjectivity and might not ameliorate bias if the remaining large studies are insufficiently critiqued. Moreover, observing heterogeneity in effects across multiple independent trials is important, even if some of these are smaller, since this is likely to reflect heterogeneity that would occur in clinical practice;. Difficulties caused by reporting biases and related small-study effects can be addressed through statistical methods of adjustment;. In this paper, we explore the levels of power available in studies included in published meta-analyses, and examine the relative influence of adequately powered and underpowered studies on these meta-analyses. Data To examine power per study within meta-analyses and to explore whether this varies across different settings, we use evidence from the Cochrane Database of Systematic Reviews ( CDSR: Issue 1, 2008), which was provided by the Nordic Cochrane Centre. Each meta-analysis was categorized by type of outcome, types of intervention compared, and medical specialty to which the research question related, as described elsewhere. In this paper, we include all meta-analyses of binary outcomes that reported data from two or more studies (14,886 meta-analyses). Calculation of Power per Study In meta-analysis j, power was calculated with respect to a fixed baseline event rate,. The median of the observed proportions experiencing events was calculated for each intervention arm separately and the higher median was used as. For each study i within meta-analysis j (with mean number of patients per treatment arm), we calculated how much power the study sample size provided to detect a relative risk reduction of 10%, 20%, 30% or 50% (or, equivalently, a relative risk of = 0.9, 0.8, 0.7 or 0.5). For convenience, we refer to a relative risk reduction of 30%, for example, as RRR30. In study i within meta-analysis j, the power to detect a difference between event rates and at a significance level of is given by: where is the cumulative standard normal distribution function and. For our primary analyses we define adequate power as ≥50% power to detect RRR30. In subsequent analyses, we fitted a random-effects model to obtain a summary relative risk estimate,, for meta-analysis j, and calculated the power of study i to detect the treatment effect observed in the meta-analysis to which it contributed, i.e. To detect a difference between and. Calculation of power per Meta-analysis The focus of this paper is on the power of primary studies within meta-analyses, but it is interesting also to examine the power of the meta-analyses themselves. In each meta-analysis j, we fitted a random-effects model, using a method-of-moments estimate for the between study variance, and calculated the variance V j of the combined intervention effect (on the log relative risk scale). The power of meta-analysis j to detect a 30% relative risk reduction or equivalently a log relative risk of, using a significance level of is given by: where is the cumulative standard normal distribution function and. Impact of Underpowered Studies We defined subset A as CDSR meta-analyses that include five or more studies, with at least two adequately powered ( ) with respect to RRR30 and at least one underpowered ( ), to investigate the impact of including or excluding underpowered studies. On the log odds ratio scale, per meta-analysis, we fitted fixed-effect and random-effects models including (1) all studies; (2) adequately powered studies only ( ) or (3) underpowered studies only ( ). For meta-analyses relating to beneficial rather than adverse outcomes, the data were rearranged, so that an odds ratio below 1 favours the experimental intervention over the comparator across all meta-analyses in subset A. A method-of-moments estimate was used for the between-study variance in the random-effects model. As a descriptive analysis of the impact of excluding underpowered studies in subset A meta-analyses, we calculated ratios comparing meta-analysis results obtained from all studies with results from adequately powered studies only. To compare effect sizes formally within subset A, we first estimated the average difference between log odds ratios in underpowered studies ( ) compared with adequately powered studies ( ) by fitting a random-effects meta-regression model. Then, in a random effects meta-analysis, we combined the estimated differences across subset A meta-analyses, with or without adjustment separately for (i) medical specialties, (ii) outcome type, (iii) intervention type. We also explored the role of underpowered studies in individual meta-analyses within a particular research setting in more detail, as described in. Power of Studies Included in Cochrane Reviews summarizes power of primary studies within meta-analyses in the CDSR database. In 10,492 (70%) of the 14,886 CDSR meta-analyses, all studies were underpowered ( ) to detect a 30% relative risk reduction ( RRR30). In many settings, a 20% relative risk reduction would be more realistic, and 85% of the meta-analyses included no studies powered to detect RRR20. Only 2,588 (17%) meta-analyses included at least two studies powered at 50% or more to detect RRR30, and only 1,291 (9%) included at least two studies powered at 80% or more. Median power within CDSR meta-analyses was low for RRR30 at 13% power, with an inter-quartile range ( iqr) of 7% to 31% power. Some studies were generously powered, with 2,571/77,237 (3.3%) having at least 98% power for RRR30 (). Percentages of 14,886 meta-analyses including no studies adequately powered to detect a target effect or including at least two adequately powered studies, where adequate power is defined as 80% or 50% in turn; and summary of median power within each meta-analysis. Power of studies to detect the summary relative risk in their meta-analysis was also low: 11,422 (77%) meta-analyses included no studies with ≥50% power and only 2,236 (15%) meta-analyses included at least two studies with ≥50% power. The median of summary relative risks was 0.75 across all meta-analyses ( iqr 0.55 to 0.89). Summarizes power for RRR30 by medical specialty, outcome and intervention-comparison type. In cancer, 35% of 689 meta-analyses included at least two adequately powered studies, and only 365 meta-analyses (53%) consisted entirely of underpowered studies. However, median power within cancer meta-analyses remained low at 24% power ( iqr 10% to 57% power). Numbers of adequately powered studies (≥50% power) and median power within each meta-analysis (MA) with respect to a 30% relative risk reduction ( RRR30), overall and by medical specialty, outcome type and intervention-comparison type. By outcome, we expected power to be lower for events that are typically rare. Power was indeed somewhat lower for meta-analyses reporting all-cause mortality and cause-specific mortality/major morbidity event/composite (mortality or morbidity), and somewhat higher for meta-analyses relating to resource use, signs/symptoms reflecting continuation/end of disease or a mixture of subjective outcomes (see ). Power of Meta-analyses Included in Cochrane Reviews summarizes the power of the meta-analyses themselves to detect a 30% relative risk reduction, overall and by medical specialty, outcome and intervention-comparison type. Overall, the proportion of meta-analyses with 80% power or more to detect RRR30 was 22%, with a further 12% powered at 50–80% to detect RRR30, but 66% were underpowered. At 34%, the proportion of adequately powered meta-analyses was substantially larger than the proportion of meta-analyses including at least two adequately powered studies, but remains low. Meta-analytic power with respect to a 30% relative risk reduction (RRR30), based on the random-effects model, overall and by medical specialty, outcome type and intervention-comparison type. The median of meta-analytic power was 27% ( iqr 11% to 72% power). There was some variation across medical areas; in cancer, 51% of meta-analyses were powered at 50% or more. Differences in meta-analytic power across medical areas, outcome and intervention-comparison types were largely in the same direction as differences in meta-analysis summaries of study power (). Ratios comparing results obtained from adequately powered studies only with results obtained from all studies, in subset A of 1,107 meta-analyses: results shown are percentiles of the distribution of such ratios across meta-analyses. Across the 1,107 meta-analyses, there was a broad spread of ratios representing changes to the summary log odds ratio. The median ratio was 0.96 for the fixed-effect model and 0.94 for the random-effects model. The results correspond to a slight shift towards the null value when underpowered studies were removed, more so under the random-effects model in which small studies have greater influence. Under the random-effects model, it is possible for precision to be gained (i.e. Smaller standard error) when studies are removed, if the heterogeneity estimate is sufficiently reduced. The non-zero between-study heterogeneity in 851 meta-analyses decreased by a median of 21% when underpowered studies were removed ( iqr −96% to +18%). Presents average differences in log odds ratios between inadequately powered ( ) and adequately powered studies, obtained from fitting meta-epidemiological models to the subset of 1,107 meta-analyses. Overall, the difference was −0.10 (95% CI −0.13 to −0.08, P. Discussion Underpowered studies made up the entirety of the evidence in most meta-analyses reported by Cochrane reviews: in 70% of CDSR meta-analyses, all studies had less than 50% power to detect a 30% relative risk reduction ( RRR30), and only 17% of meta-analyses included at least two studies with at least 50% power for RRR30. There was some variation across medical areas and outcome types, but individual studies’ power was low across all types of meta-analyses. In a meta-epidemiological analysis of 1,107 meta-analyses, we found that odds ratios in underpowered studies were on average 10% lower (95% CI 8% to 12%, P. References • 1. Sterne JAC, Gavaghan D, Egger M (2000) Publication and related bias in meta-analysis: power of statistical tests and prevalence in the literature. Journal of Clinical Epidemiology 53: 1119–29. Nygard O, Vollset SE, Refsum H, Stensvold I, Tverdal A, et al. (1995) Total plasma homocysteine and cardiovascular risk profile. JAMA 274: 1526–33. Kjaergard LL, Villumsen J, Gluud C (2001) Reported methodologic quality and discrepancies between large and small randomized trials in meta-analyses. Annals of Internal Medicine 135: 982–9. Stanley TD, Jarrell SB, Doucouliagos H (2010) Could it be better to discard 90% of the data? A statistical paradox. The American Statistician 64: 70–7. Kraemer HC, Gardner C, Brooks III JO, Yesavage JA (1998) Advantages of excluding underpowered studies in meta-analysis: inclusionist versus exclusionist viewpoints. Psychological Methods 3: 23–31. Merrall ELC, Kariminia A, Binswanger IA, Hobbs MS, Farrell M, et al. (2010) Meta-analysis of drug-related deaths soon after release from prison. Addiction 105: 1545–54. Halpern SD, Karlawish JHT, Berlin JA (2002) The continuing unethical conduct of underpowered clinical trials. JAMA 288: 358–62. Edwards SJL, Lilford RJ, Braunholtz D, Jackson J (1997) Why “underpowered” trials are not necessarily unethical. The Lancet 350: 804–7. Guyatt GH, Mills EJ, Elbourne D (2008) In the era of systematic reviews, does the size of an individual trial still matter? PLoS Medicine 5(1): e4. Altman DG (1994) The scandal of poor medical research. BMJ 308: 283. Turner RM, Spiegelhalter DJ, Smith GCS, Thompson SG (2009) Bias modelling in evidence synthesis. Journal of the Royal Statistical Society, Series A 172: 21–47. Shrier I, Platt RW, Steele RJ (2007) Mega-trials vs. Meta-analysis: precision vs. Contemporary Clinical Trials 28: 324–8. Borm GF, Lemmers O, Fransen J, Donders R (2009) The evidence provided by a single trial is less reliable than its statistical analysis suggests. Journal of Clinical Epidemiology 62: 711–5. Moreno SG, Sutton AJ, Ades AE, Stanley TD, Abrams KR, et al. (2009) Assessment of regression-based methods to adjust for publication bias through a comprehensive simulation study. BMC Medical Research Methodology 9(2). Rucker G, Carpenter JR, Schwarzer G (2011) Detecting and adjusting for small-study effects in meta-analysis. Biometrical Journal 53: 351–68. Davey J, Turner RM, Clarke MJ, Higgins JPT (2011) Characteristics of meta-analyses and their component studies in the Cochrane Database of Systematic Reviews: a cross-sectional, descriptive analysis. BMC Medical Research Methodology 11: 160. DerSimonian R, Laird N (1986) Meta-analysis in clinical trials. Controlled Clinical Trials 7: 177–88. Hedges LV, Pigott TD (2001) The power of statistical tests in meta-analysis. Psychological Methods 6: 203–17. Wetterslev JTK, Brok J, Gluud C (2008) Trial sequential analysis may establish when firm evidence is reached in cumulative meta-analysis. Journal of Clinical Epidemiology 61: 64–75. Brok J, Thorlund K, Gluud C, Wetterslev J (2008) Trial sequential analysis reveals insufficient information size and potentially false positive results in many meta-analyses. Journal of Clinical Epidemiology 61: 763–9. Thorlund K, Imberger G, Walsh M, Chu R, Gluud C, et al. (2011) The number of patients and events required to limit the risk of overestimation of intervention effects in meta-analysis - a simulation study. PLoS ONE 6(10): e25491. Charles P, Giraudeau B, Dechartres A, Baron G, Ravaud P (2009) Reporting of sample size calculation in randomised controlled trials: review. BMJ 338: b1732. Nuesch E, Trelle S, Reichenbach S, Rutjes AWS, Tschannen B, et al. (2010) Small study effects in meta-analyses of osteoarthritis trials: meta-epidemiological study. BMJ 341: c3515. Sterne JAC, Sutton AJ, Ioannidis JPA, Terrin N, Jones DR, et al. (2011) Recommendations for examining and interpreting funnel plot asymmetry in meta-analyses of randomised controlled trials. BMJ 343: d4002. Watt A, Cameron A, Sturm L, Lathlean T, Babidge W, et al. (2008) Rapid reviews versus full systematic reviews: an inventory of current methods and practice in health technology assessment. International Journal of Technology Assessment in Health Care 24: 133–9. Software - revenge email spam list. Easy Email Spam Filter, List Cleaner Intravenous, Jvw filter email. • In the search box at the top, click the Down arrow. • Enter your search criteria. 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Unsourced material may be challenged and removed. (March 2013) () A recovery point objective (RPO) is defined. It is the maximum targeted period in which might be lost from an IT service due to a major incident. The RPO gives systems designers a limit to work to. For instance, if the RPO is set to four hours, then in practice, off-site mirrored backups must be continuously maintained – a daily off-site backup on tape will not suffice. ![]() Contents • • • • • Background [ ] When IT systems used for normal business services are affected by a major incident that cannot be fixed quickly, the business will want to restore the state of the systems to a known, consistent point that is as up-to-date as possible. The business should have an Information Technology Service Continuity (ITSC) Plan that covers such scenarios, and realistically achievable objectives for the restoration of the service. This plan should usually assume that the production computing equipment and the wider geographic location where they normally reside might become completely out of bounds at an unpredictable time, without any warning. The location chosen from which to run the restored service (the recovery site) ought to be distant (for example, at least 10 miles) from the normal production site and to suffer no threats in common with it (e.g. They should not be near the same coastline). RPO (and RTO) [ ] The ITSC Plan must also satisfy two measurements for any potentially affected services: Recovery Point Objective (RPO) and the. They specify time intervals, typically expressed as a number of hours, relating to loss of data (recent transactions) and loss of service time. They are both compromises, often largely determined by business impact costs: minimising these times is increasingly cheaper in adverse business impact but increasingly expensive to implement. 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Delaware Florida RTO Pro Software Delaware SENATE Chief of Staff Jim Reilly Scheduler: Aaron Walls Legislative Director: Bill Ghent Communications Dir: Bette Phelan Born: March 15, 1939 Educational Experience: MBA, Wharton School Assumed Office:. ![]() ![]() The associated risk assessments include potential loss of life of the knowledgeable people who ran the prior service. The RTO is the amount of time the business can be without the service, without incurring significant risks or significant losses. The events that mark the start and end of the RTO duration must be pre-agreed between Business Continuity and ITSC staff. It may be defined as the interval from breakage of the service to its full restoration to the customers. Alternatively the start of the interval might be determined as moment when it is decided to proceed with the recovery, and the end as the moment when the team responsible for testing the service (before it is successfully released to the wider user community) begin work. Defining the RTO in this way can permit better decision making at all levels, although it compromises its measuring 'the amount of time the business can be without the service'. The RPO measures the maximum time period in which recent data might have been permanently lost in the event of a major incident; it is not a direct measure of the quantity of such loss. ![]() For instance if the BC plan is 'restore up to last available backup', the RPO is the maximum interval between such backup that has been safely vaulted offsite. Two points should be noted. Firstly, is used to determine RPO for each service – RPO is not determined by the existent backup regime. Secondly, when any level of preparation of off-site data is required, the period during which data often starts near the time of the beginning of the work to prepare backups, not the time the backups are taken off-site. Data synchronization points [ ] A data synchronization point is a point in time. It is used to assess the way in which data backups relate to each other. Data backups need to be related to each other correctly when considering the time of day they were made, or their relationship to computer system activity events. A data synchronization point is a point in time when a set of backups exist which if restored from can be synchronized to the same point in time. Often this point in time is some hours before the last backup is completed, i.e., some hours before the data synchronization point. Backups that have no synchronization points are generally useless. A frequent mistake when setting RPO for traditional daily tape offsited backups is to assume 24 hours for the RPO. This mistake is the result of not considering that the RPO time begins with the start of the first data backup used in the synchronization point; and must also include time for boxing the tapes; the inevitable contingency time that must be allowed for 'waiting for courier transport'; loading and final escape from site (not always at exactly the same time of day – the RPO must be increased by an amount of time equivalent to any such variability). It is also risky to assume that tapes will always be physically intact – the RPO should include enough time to use a previous synchronization point, too. How RTO and RPO values affect computer system design [ ] The RTO and RPO form part of the first specification for any IT Service. The RTO and the RPO have a very significant effect on the design of computer services and for this reason must be considered in concert with all the other major system design criteria. When assessing the abilities of system designs to meet RPO criteria, for practical reasons, the RPO capability in a proposed design is tied to the times backups are sent offsite- if for instance offsiting is on tape and only daily (still quite common), then 49 or better, 73 hours is the best RPO the proposed system can deliver, so as to cover for tape hardware problems (tape failure is still too frequent, one bad tape can write off a whole daily synchronisation point). Another example- if a service is to be properly set up to restart from any point (data is capable of synchronisation at all times) and offsiting is via synchronous copies to an offsite mirror data storage device, then the RPO capability of the proposed service is to all intents and purposes 0 hours- although it is normal to allow an hour for RPO in this circumstance to cover off any unforeseen difficulty. If the RTO and RPO can be set to be more than 73 hours then daily backups to tapes (or other transportable media), that are then couriered on a daily basis to an offsite location, comfortably covers backup needs at a relatively low cost. Recovery can be enacted at a predetermined site. Very often this site will be one belonging to a specialist recovery company who can more cheaply provide serviced floor space and hardware as required in recovery because it manages the risks to its clients and carefully shares (or 'syndicates') hardware between them, according to these risks. If the RTO is set to 4 hours and the RPO to 1 hour, then a mirror copy of production data must be continuously maintained at the recovery site and close to dedicated recovery hardware must be available at the recovery site- hardware that is always capable of being pressed into service within 30 minutes or so. These shorter RTO and RPO settings demand a fundamentally different hardware design- which is for instance, relatively much more expensive than tape backup designs. If very high volumes of high value transactions are to be planned for, then the production hardware can be split across two sites; with a high bandwidth network connection between the two sites constant mirroring of data can be achieved. If the user community is dispersed or at least split across two geographic areas, then the configuration is resilient to single site Major Incidents- with zero RTO and RPO being achievable, and very often little loss of service being experienced at most times of day. References [ ]. 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