The causes of PBIS are well known, consisting of various decisions about reporting that are influenced by the data. But its impact is not generally appreciated, and very little attention is devoted to it. What attention there is consists largely of rules for statistical analysis that are impractical and do not actually reduce the bias in reported estimates. PBIS cannot be reduced by statistical tools because it is not fundamentally a problem of statistics, but rather of non-statistical choices and plain language interpretations. PBIS should be recognized as a phenomenon worthy of study – it is extremely common and probably has a huge impact on results reported in the literature – and there should be greater systematic efforts to identify and reduce it. The paper presents examples, including results of a recent HIV vaccine trial, that show how easily PBIS can have a large impact on reported results, as well as how there can be no simple answer to it.PBIS is a major problem, worthy of substantially more attention than it receives. There are ways to reduce the bias, but they are very seldom employed because they are largely unrecognized. A study is more likely to appear in the literature, and thus be indexed and publicly available, if it shows a strong, statistically significant, or otherwise "better" result. A study that does not show such results has a greater chance of remaining hidden in a file drawer, either because the author (or funder) does not think the result is worth mentioning, or because journals are less interested in publishing studies that find "nothing". This form of publication bias, wherein readers have access to only a biased sample of the full distribution of results, is well studied, particularly in the literature on meta-analysis and other systematic reviews where the problem is most apparent (a primer on the topic can be found at the Cochrane Collaboration webpage ). Even wwhich results to publish produces bias. As with traditional publication bias, the tendency is to analyze data and choose to present results which are statistically significant, further from the null, or closer to what the researchers believe is the true value. The implications for the literature as a whole, though, are much the same as the file drawer bias. I label this "publication bias in situ" (PBIS) because the biased reporting of study findings exists within each individual research report . Despite the similarities between the file drawer bias and PBIS, there are fundamental differences. In particular, the bias from some studies having no published findings exists only at the level of the whole literature (no particular study can be said to be biased), while PBIS exists within the results reported from a single study (and thus exists in the literature as a whole by aggregation). More practically, PBIS is substantially more difficult to even identify, let alone correct.Far less attention is paid to the bias that occurs when some results from a study are published, but the choice of This paper defines and describes PBIS and identifies some of the choices that create it. The purpose of the paper is not to make novel technical or statistical claims. Indeed, there is probably no single statistical observation here that will not be clear to a skilled data analyst . The literature includes many observations about issues relating to PBIS. Yet the challenge to the validity of the entire health science literature posed by PBIS – arguably a greater issue than conflict of interest, traditional publication bias, or any other commonly discussed threat to the integrity of the literature – has not received the attention it deserves.ex ante protocols were stated and followed, and is thus put on par with many protocol violations that could be considered mere technicalities. For example, a few years ago, a highly-publicized meta-analysis [In the literature about meta-analysis and systematic reviews there is substantial attention to file-drawer publication bias . But there is considerably less attention to possible picking and choosing which study results to report or statistical methods to use. To the extent that this is considered, it is often bundled with questions about whether analysis  called iThe literature and pedagogy related to observational inference, where the potential for PBIS is considerably greater than for well-designed experiments, seems to pay even less attention. Epidemiology textbooks typically discuss some of the methods that can reduce PBIS , but say little or nothing about the possible bias. Indeed, many study and data-analysis methodologies (some of which are noted below) that are typically taught in classes or by apprenticeship seem designed to create PBIS. Despite this, highly-trained experts summarize claims reported in the literature without mention of the likely bias, indicating an unawareness of the major implications of PBIS.In a notable exception, Hahn and colleagues ,4 discusIt is not clear how common PBIS is or how large the resulting bias, but a few efforts to find it suggest that the potential is great enough that it deserves much more attention.  Only by systematically addressing the problem are we likely to substantially affect it. Moreover, as will be discussed, statistical and research methods that ostensibly address some of the sources of PBIS are unsatisfactory, and a systematic attempt should be made to find better solutions.Reviewers (systematic or otherwise) of the literature can only see what researchers choose to report and highlight in their publications, and that choice can be biased in a number of ways. Researchers have great freedom in deciding exactly what to analyze, how to analyze it, and what to report. All research results are derived from data that can be used to measure many associations. Even the most narrowly focused clinical trial can be analyzed with the endpoint defined in different ways, stratified by age, etc. As with traditionally defined publication bias, the analyses that are deemed unworthy of publication are largely invisible to the scientific and policy community.Among the dimensions of freedom researchers have in deciding what to analyze and report are three choices illustrated by examples in this paper:(1) Which exposures and outcomes to consider in datasets with many variables.(2) Which functional forms to use to represent variables .(3) Whether to conduct separate analyses by subgroup, and which subgroup results to emphasize.some question), there is no clearly wrong choice, and thus no clear way of concluding that a particular choice was biased. Fortunately, as should become apparent from the following analysis, PBIS results less from the choices made and more from what the choices are based on (which can often be inferred) and, to an even greater extent, the generally overlooked issue of how the results are presented (which can be easily observed).Making such choices is a legitimate part of research. Indeed, the choices must be made. But when those choices are primarily driven by what produces stronger (or otherwise "better") results, bias is created. This creates a difficult challenge: It is easy to recognize traditional publication bias . But since there is no clearly correct option for any of the above choices , creating a bias from what would be unbiased random variation. Systematic errors  and methods for correcting for them create many additional opportunities for PBIS; however, for simplicity, systematic errors are ignored in this paper.Choice (1) in the above list has probably received the most attention in previous literature . Despite the disproportionate attention, this choice is probably not the major source of PBIS, but it provides a familiar starting point.Many epidemiologic datasets are characterized by thousands or even millions of possible combinations of exposures, endpoints, and covariates. It is frequently assumed that statistical science tells us the "right" way to deal with this challenge, but current practice (not to mention the confusion of students coming out of epidemiology and biostatistics classes) makes clear that there is substantial disagreement among viewpoints about how to apply statistical methods when dealing with multiple hypotheses or measurements. Further consideration makes it clear that statistical rules cannot actually provide clear answers.At one extreme are viewpoints such as, "We must correct measures of statistical certainty  or confidence interval widths) whenever multiple comparisons are made using the same dataset" and even, "statistical analysis can only be legitimate for a short list of pre-specified hypotheses." At the other extreme are viewpoints such as, "regardless of how many comparisons are examined, each can be considered and statistically tested as if it were the only one," and, "it does not matter at all if a hypothesis was proposed after looking at the data." The impasse in this debate seems to stem from both sides attacking straw men, without recognizing that each side has a stronger case some of the time. This can be illustrated with examples.Helicobactor pylori infection contains data that is later used to look at the relationship of household crowding and performance in school. It is difficult to understand why we would make an adjustment when doing the second analysis because we have already done the first . A logical extension of that argument would be to consider the dataset that contains all quantitative human knowledge , and declare that we have to adjust for every statistical analysis ever done, effectively precluding further statistical analysis.A cohort dataset originally used to report the relationship of drinking water source and the occurrence of H. pylori infection. The dataset contains dozens of different measures of food and nutrient intake, as is usually the case for nutrition data. This, plus multiple diagnostic tests for H. pylori which are sometimes discordant, creates a large number of statistical comparisons, any of which could be described as supporting the plain language claim, "poor nutrition affects H. pylori status." A typical approach is to find individual comparisons that support the hypothesis, presenting only these comparisons with statistical tests as if each were the only analysis conducted. The claim about the relationship between the particular measure of nutritional status and the particular measure of H. pylori status is accurate, as are the test statistics reported for that association. But the plain language conclusion (which would probably be drawn) was very likely to be supported by some relationship in the data by chance alone, even in the absence of any true underlying association. This fact is obscured by the reported unadjusted tests statistics or confidence intervals.Researchers investigate the hypothesis that poor nutrition increases the risk of in situ within a single published article, making it a bias of much greater magnitude than the file-drawer effect).As the second example illustrates, unrestricted picking and choosing of comparisons leads to publication bias. A lot of associations that were not deemed worthy of reporting never appeared in the literature, while the few that were "interesting" did. This problem is well known , correcting for multiple comparisons does not affect the reported biased estimates of effect size; changing test statistics and confidence interval widths does nothing to reduce the bias. This alone shows that the standard statistical corrections for multiple tests do nothing to solve the problem. The other standard method for trying to reduce PBIS, rules that limit analyses to pre-specified hypotheses and protocols, will throw away a lot of potentially valuable findings and is nearly impossible to operationalize because detailed protocols require advanced knowledge that may not exist and can never be specified unambiguously.The solutions offered by statistical rules – corrections for multiple hypothesis testing or restricting analysis to Frequentist statistical theory cannot offer a solution to this problem because PBIS, like the file-drawer problem, is not a matter of statistics. The second example illustrates where the problem primarily lies: in the plain-language reporting of results. The statistics that describe the relationship between a particular exposure and outcome measure could be exactly right, but the claim about good nutrition (as a generic concept) and infection status (as if we had a gold standard measure), which will likely be emphasized in the paper and its title (and press releases) and will likely stick readers' minds, might be misleading. Consider how the result would be interpreted if there were a table reporting every analyzed comparison, most of which showed little or no association. Most scientifically literate readers would realize the result was not so convincing, even though those same readers seldom think to object when – as is typical – only one or a few results are reported. By contrast, if the researchers in the first example reported the result of the previous study, it would be unlikely to change most readers' assessments.ex ante hypothesis or having "used up" the α), but without creating the PBIS that would result otherwise. Indeed, this appears to summarize the most obvious generic rule to reduce PBIS : publish everything.This suggests the simplest partial solution to the problem. By reporting a table of results from other comparisons considered, researchers could report their interesting result , and can include dozens or thousands of alternative analyses in appendices or links to data or software that allow the reader to review still more results. Of course, this opportunity is beneficial only if authors choose to take advantage of it (or editors and reviewers demand that they do).The implications of choice (2), the functional form for variables, can be clearly illustrated with a simple example. Consider a study with an exposure variable measured as 10 ordered categories . Assume researchers wish to analyze the association of a disease endpoint and a dichotomous definition of exposure. If there is no clear cutpoint for defining exposure, there are many options. There are 9 cutpoints that divide the observations into two categories, defining those above the cutpoint to be exposed and those below unexposed. Other options include comparing a group of highest categories to a group of lowest categories, leaving out the middle, such as 8–10 versus 1–3, yielding an additional 36 possibilities.How will the researchers choose a definition of exposure? A typical procedure is to let the data inform the choice: The cutpoint that provides the clearest contrast between the exposed and unexposed is judged to be the right one, the "most sensitive" to the presumed effect. It should be immediately obvious that this procedure will bias the result away from the null.To illustrate this, consider a case-control study with 200 subjects . Calculations for this example and others are based on Monte Carlo simulation of different realizations of the data based on the assumed underlying relationship. All simulations were performed using Crystal Ball .Assume that each of the 10 exposure categories is equally likely for cases and non-cases. If the researchers consider only the 9 cutpoints that dichotomize the data and choose the cutpoint for "exposed" to get the largest odds ratio (OR), the median result will be 1.5. Since the exposure and disease are not associated, this is clearly an upward bias. For those inclined to focus on statistical significance, the chance of observing a significant positive association at a one-tailed significance level of .025 is 13%. Even if researchers do not analyze their data in every possible way and report the strongest association, any decision to report results that is based on associations in the data  will create bias. Although this observation should be obvious to anyone with an understanding of statistics, letting the data have some influence on the choice is probably more the rule than the exception among researchers. It is often defended on the grounds that there was no way to know what the "right" cutpoint was before doing the study, and the study data is the only existing answer to the question. This is a legitimate point, but it does not reduce the resulting bias. Less scrupulous researchers – who are trying to support a preferred answer to further a policy agenda or advance their careers – need make no such explanation and can intentionally choose the extreme results.As with the file-drawer effect, results in the literature will tend to show effects greater than the true value. Most important, whichever analysis is reported, the plain-language result will be "we found an association between the exposure and the disease," and so collections of studies that each report an exposure-disease comparison with a greater-than-average association, and will seem to be confirming the same result, even though the comparisons are not the same.Extending this example to illustrate how PBIS can compare to traditional publication bias, assume now that there is a positive association between the exposure and disease. In particular, non-cases are still equally likely to be in each of the ten categories, while cases have respective probabilities for each category of . These values were chosen so that the true OR is similar, whichever of the 9 cutpoints is chosen . True ORs round to 1.5 for all cutpoints.Consider a collection of studies of varying sizes, with fewer larger studies, as we would typically see in the literature, specifically 100 randomly generated studies  of random size . Note that to avoid committing the very type of transgression discussed in this paper – repeating an analysis until "good" results are found – the reported results are from the first and only run of the simulation.For a single definition of "exposed" values >5), a typical result appears in Figure , a typicCompare this to the results for the same 100 studies where the cutpoint is chosen based on the largest OR Figure . The disUnbiased random errors, when combined with picking and choosing functional forms, lead to biases in reported results. A solution to this problem is much less obvious than its existence.The commonly proposed solution of only reporting results for pre-specified functional forms is not satisfactory, because it is difficult to enforce  and it forces us to ignore real unpredicted findings. Sticking to pre-specified analyses is especially unrealistic in research studies that collect data on many different risk factors and outcomes. Simply labeling all results that were not pre-specified with the caveat, "hypothesis generating," accomplishes nothing. If such results were actually treated as not yet "real", the problems of determining exactly which results were pre-specified and the loss of important serendipitous findings are reintroduced. Of course, results with the caveat are very seldom treated as less real than any others in the literature. Moreover, the "generated" hypotheses will never be retested in exactly the form reported, so the label is simply disingenuous. In sum, the proposed solutions to this type of PBIS are no more realistic or satisfactory as solutions than trying to eliminate traditional publication bias by requiring that all studies be adequately powered.A better family of solutions would be to establish a standard of reporting results for alternative variable definitions (perhaps in online appendices). Not only does this directly reduce PBIS by publishing more results, but it provides readers with a choice of results if they prefer different definitions (information that would be discarded by a pre-specified hypothesis rule). If results for every cutpoint from the 100 trials in the example were reported, the results, as pictured in Figure In many cases there will not be an obvious short list of variable definitions, but some alternative definitions should be obvious and others could be found in previous literature. A simple, but very useful, improvement would be a standard practice of reporting the closest possible replication of previous published analyses using data from the new study. This would directly address the problem of PBIS resulting from data-driven picking and choosing of functional forms . Repeating whatever analyses that previous researchers happened to choose is somewhat arbitrary, but each round of new research can also add a new preferred functional form. The key is that results based on previously published functional forms cannot be data driven and, unlike the standard practice of new studies that make different comparisons but describe them with the same plain language, would actually replicate (or fail to replicate) previous results.New York Times articles actually contained more complete study results. VaxGen tried to salvage some hope for the drug by pointing out the results for non-whites, suggesting that maybe it held promise for some populations [In 2003, VaxGen Corporation  released results of a large HIV vaccine trial in the United States, one of the highest-profile clinical trials of the year. The disappointing result showed a trivial reduction in incidence among the treatment group compared to the placebo group. But the three non-white racial groups  each showed a substantial reduction in incidence Table . VaxGen ulations . VaxGen'ulations -12.Given the failure to publish the results in a scientific journal, some might argue that VaxGen was guilty of traditional publication bias – not publishing unfavorable results about its products – a charge that is currently being leveled at many drug companies. However, the company actively released fairly complete study results and accompanying analysis to the press, and the results appeared in forums that are more widely read than all scientific journals combined, so the results were clearly not buried in a file drawer.But despite reporting their results, VaxGen was biasing what they published. Singling out of the result for non-whites is a clear case of PBIS. VaxGen did not give equal emphasis to the apparently harmful effect of the vaccine for whites. The company's subsequent report that the different results for whites and non-whites could not be due to chance  does not4-1 = 15 different hypotheses. To adjust for 15 implicit hypotheses makes it very unlikely that any will pass the statistical test, including the population as a whole, even for substantial associations.Setting aside some controversy that erupted about systematic errors in the data, what can we say about the results from the perspective of PBIS and chance alone? To look at the result for non-whites, with its one-tailed p-value of .002, ignoring the fact that the subgroup definition was clearly data-driven, would overstate the finding, as suggested in the preceding examples. But a naive correction for multiple hypothesis testing would make the opposite error. Setting aside the possibility that other covariates would have been used to stratify the data had they produced subgroups with positive findings, the combination of the 4 racial groups implies a test of 2An alternative is to ask the question, "if the vaccine has no effect, what are the chances of seeing, in any racial group or combination thereof, a result at least as strong as the observed 63% reduction?". Phrased that broadly, simulation shows the answer is about 20%. However, most of the 20% comes from the unstable results for the two smallest groups, Asians and "other". Restricting the analysis to combinations of racial groups that contain black, with or without Asians or other, the probability is only 2.1% .So, what is the right answer? We must return to the observation that there is never a single Right Answer from a study; the quality of an answer always depends on what question was being asked. Did VaxGen find a successful vaccine? Clearly not, as the relative risk for the whole population shows. Should the result for non-whites be considered unlikely to be due to chance ? It depends on whether you consider it the answer to the question "does the vaccine show a result for non-whites?", in which case the answer is 'yes' , or "does the vaccine show a result for any racial group?" in which case the answer is 'it is fairly likely we would see such a result due to chance alone.' It is worth noting how this illustrates a popular fallacy in data analysis: Frequentist hypothesis testing is not the objective exercise that some think it to be; it depends on subjective decisions about what to test.ex ante hypothesis that the vaccine would work only in non-whites or because the multiple-hypothesis correction for hundreds of possible racial and other subgroups makes it non-significant. A general rule requiring us to ignore interesting but surprising findings is a huge waste of information. Requiring a data-driven subgroup analysis to be biologically plausible before reporting it offers no solution, since we can usually construct a story to explain whatever associations appear in the data .We might decide to infer that VaxGen would have emphasized the results from any racial subgroup that showed a positive result , and thex ante plan to analyze racial and other subgroups [ex ante, as if that should change our interpretation of the result, seems particularly absurd.To offer the "hypothesis generating" caveat would make little difference, scientifically or in the securities market. It is unrealistic to suggest that this "generated" hypothesis will be re-examined given the overall disappointing result. Two studies in Thailand  that suggests there is a beneficial effect for some people should equally emphasize any apparent harmful effects for other people (and vice versa). The fact that one result is statistically significant and the other is not should be of no consequence. Indeed, selecting which results to report based on statistical significance guarantees there will be publication bias . The reporting of the multiple subgroups results should be accompanied by statistics similar to those calculated here, instead of standard test statistics, so that readers know the probability that an estimated effect (or test statistic) at least as great as the one found would result from chance alone for any of the subgroup analyses. Such information will allow readers  to focus on what they consider to be the answer to their own questions.The opportunities for PBIS, along with the almost universal failure to report research results in ways that avoid it, create the possibility that biased study results are very prevalent in the health science literature. Some of the causes of PBIS are well understood, but the enormity of its implications is largely ignored.PBIS can produce very misleading results, leading to widespread misperceptions and misguided policies. The examples presented here show just a few of the many ways that PBIS can result from random error and researchers'  choices. Neither the problem nor the solution lies in the mathematics of data analysis, so answers will not be found by appealing to statistical theory. The critical issue is the completeness of reporting and the plain-language interpretation of results.The simple solutions offered by statisticians are not satisfying or even realistic. All they really let us do is observe that in almost every research report, "the rules" have been violated. This is not helpful. Rather than a right-vs.-wrong view of proper use of statistics that would condemn most of the literature as invalid, we need a realistic way of addressing this problem. The solutions, like the solutions for traditional publication bias, will generally consist of doing a more complete job of reporting what can be reported.HIV = human immunodeficiency virusOR = odds ratioin situPBIS = publication bias None declaredSingle authorThe pre-publication history for this paper can be accessed here:


To determine whether previously reported loci predisposing to nonsyndromic high myopia show linkage to common myopia in pedigrees from two ethnic groups: Ashkenazi Jewish and Amish. We hypothesized that these high myopia loci might exhibit allelic heterogeneity and be responsible for moderate /mild or common myopia.Cycloplegic and manifest refraction were performed on 38 Jewish and 40 Amish families. Individuals with at least -1.00 D in each meridian of both eyes were classified as myopic. Genomic DNA was genotyped with 12 markers on chromosomes 12q21-23 and 18p11.3. Parametric and nonparametric linkage analyses were conducted to determine whether susceptibility alleles at these loci are important in families with less severe, clinical forms of myopia.There was no strong evidence of linkage of common myopia to these candidate regions: all two-point and multipoint heterogeneity LOD scores were < 1.0 and non-parametric linkage p-values were > 0.01. However, one Amish family showed slight evidence of linkage (LOD>1.0) on 12q; another 3 Amish families each gave LOD >1.0 on 18p; and 3 Jewish families each gave LOD >1.0 on 12q.Significant evidence of linkage (LOD> 3) of myopia was not found on chromosome 18p or 12q loci in these families. These results suggest that these loci do not play a major role in the causation of common myopia in our families studied. Myopia is one of the leading causes of vision loss around the world. In the Despite many decades of research, little is known about the precise molecular defects and abnormal biochemical pathways that result in myopia. Compelling data from familial aggregation and twin studies indicate that susceptibility to myopia is inherited. Several familial aggregation studies have reported a greater prevalence of myopia in children of myopic parents compared to children of nonmyopic parents -12. SeveThe combination of genetic and environmental influences on the development of myopia suggests that myopia is a complex disorder and should not be classified as a simple Mendelian trait. Further evidence is shown by studies that have reported correlation coefficients for myopia between offspring and parents and between pairs of siblings to lie between 0.07–0.36 -32. Due To avoid some of the complexity in mapping genes for myopia we have collected refractive measurements and DNA samples from Amish and orthodox Jewish families with myopia. The Old Order Amish are mostly rural farmers and craftsmen. They lead a culturally and technologically distinct lifestyle. They are a genetically well-defined founder population with large families and well-documented genealogies ,35. FamiThe orthodox Jewish families in this study are all of Ashkenazi descent, a population with known founder effects in other common diseases. This poThe study protocol adhered to the tenet of the Declaration of Helsinki and was approved by the University of Pennsylvania and the National Human Genome Research Institute, National Institutes of Health institutional review boards. Informed consent was obtained from the subjects after explanation of the nature and possible consequences of the study. The collection of orthodox Jewish individuals was begun by a mass mailing of 3900 letters to all the known orthodox Jewish families living in Lakewood, New Jersey. Questionnaires were sent with letters explaining the study. If willing to participate, individuals completed and returned questionnaires that included their contact and physician information. Second and third mailings went out to individuals who did not respond – either positively or negatively – to the first mailing. The total number of questionnaires returned was 1,310. All Jewish individuals included in the study were of Ashkenazi heritage. Collection of Amish families was done by an advertisement in an Amish newspaper, referrals from local eye doctors in the Lancaster County community and word of mouth. Criteria for entry into the study included the following: 1) Negative history of systemic or ocular disease which may predispose to myopia, 2) negative history of a premature birth, 3) proband must be affected and must have a family history of myopia in either their parents or children, 4) only one parent (as opposed to both parents) of the proband can be myopic. For the Orthodox Jewish population, an individual's myopic status was obtained from the most recent (within 2 years) measurement of refractive error. If not recent, an individual was given a repeat exam by their local eye doctor or one of the study investigators (D.S.). For the Amish subjects, all participants were examined by a study investigator (D.S.) at the Amish Eye Clinic in Strasburg, PA. Amish participants were brought to the study site because they do not have phone access making it difficult to obtain a past history and records. Cycloplegic refractions were done on all individuals less than 40 years of age with one drop each of 1% cyclogyl, 1% mydriacyl and 2.5% phenylephrine. A manifest refraction was performed if an individual was older than 40 years of age. Classification as myopic required at least -1.00D in each meridian of both eyes. Individuals were classified as nonmyopes if they were over 21 years of age and did not meet the above criteria for myopia. Other individuals were classified as nonmyopic if they were 5–10 years old and had ≥ +3.00D in each meridian, 10–18 years old with ≥ +2.00D in each meridian or 18–21 years old with ≥ +0.50D in each meridian. All other individuals were classified as unknown for the trait.This ascertainment protocol resulted in the collection of 40 Amish families and 38 orthodox Jewish families. Of the 40 Amish families, phenotype data were available on 340 persons  but only 323 DNA samples were available to be genotyped. In the 38 Jewish families, phenotype data were available for 313 persons  and DNA samples were available and genotyped for 290 of these family members.2; 10 mM Tris/HCl (pH8.3); 50 mM KCl; 0.6 uM of each primer; and 7.6 units/ul of Taq polymerase. Standard thermocycling was as follows: 94°C for 30 sec., 55°C for 30 sec. and 72°C extension time for 30 sec. Markers used included D12S85, D12S1706, D12S346, D12S78, D12S79, D12S86, D18S59, D18S481, D18S63, D18S452, D18S53, and D18S474 located in the 18p and 12q regions implicated in high myopia [Peripheral blood was collected from family members. High molecular weight genomic DNA extraction from the blood samples was performed with a kit . Polymerase chain reactions were performed in a 17.05 ul volume containing 12–320 ng/ul of DNA; 880 uM each of dATP, dCTP, dGTP, and dTTP; 3 mM MgClh myopia ,17.A simulation study was conducted on the first 44 Ashkenazi Jewish families collected in this study, using the computer program SIMLINK ,39, to c: D12S85-42.78-D12S1706-0.53-D12S346-7.22-D12S78-13.44-D12S79-9.23-D12S86; D18S59-6.94-D18S481-1.36-D18S63-10.4-D18S452-22.54-D18S53-30.08-D18S474. To carefully explore the possibility of linkage of common myopia to these high myopia candidate regions, we utilized 12 different parametric models  divided by the square root of the total number of families (N = 78)[The data on 40 Amish and 38 Ashkenazi Jewish families were checked for misspecification of family structures, data entry errors and genotyping errors using the program SIBPAIR,42 and tAs expected, the estimated average maximum LOD score decreases with the distance between the linked marker locus and the trait locus, and with increasing heterogeneity. However, only minimal changes in projected power for our Ashkenazi families were observed as penetrance, phenocopy rate and disease allele were varied. Projected power was always higher when an allele frequency of 0.01 was used for the susceptibility allele at the trait locus than when an allele frequency of 0.05 was used; however, these differences in power were very small. Table Parametric and nonparametric LOD scores were calculated for 40 Amish pedigrees and 38 Jewish pedigrees. The six markers on chromosome 12q21-q23 spanned 73 cM, and the six markers on chromosome 18p11.2-p11.32 spanned 70 cM. Markers D12S1706, D12S346, D18S59, D18S481 and D18S63 were previously reported by Young et al. ,17 as shResults of two-point parametric linkage analysis of myopia assuming linkage heterogeneity to the chromosome 12 and 18 markers in 40 Amish families are presented in Table The same markers on chromosome 12q21-q23 and chromosome 18p11.2-p11.32 were analyzed using 38 Ashkenazi Jewish families Table . StatistHeterogeneity testing using HOMOG in the combined Jewish and Amish families also did not yield any significant evidence of linkage in these two regions, with the maximum HLOD's being 0.39 and 0.95 on chromosomes 12 and 18 respectively.p = 0.09 but was not close to the significance level of at least p = 0.01 needed to provide confirmation of a prior linkage[Furthermore, nonparametric two-point NPL scores did not show any significant evidence for linkage in either the Amish or Jewish populations. The observed combined NPL score of 1.37 for D12S1706 approached nominal significance at r linkage.Multipoint parametric linkage analyses assuming homogeneity were consistently negative in both the Amish and Jewish datasets. A maximum multipoint parametric HLOD of 0.92 was observed at D18S474 in the Amish population. However, multipoint parametric HLOD scores were essentially zero for the chromosome 12 region in the Amish and for both the chromosome 12 and 18 regions in the Jewish families.p = 0.05)  showed marginal evidence for linkage (LOD > 1.0) to the region previously reported on chromosome 12 (D12S1706 and D12S346) for both two-point and multipoint parametric analyses Table . Three AThe overall results of these preliminary studies do not indicate any strong evidence for linkage of myopia in these families to the candidate regions on chromosomes 12 or 18. Although some families show marginal evidence of linkage to one of these regions, the results could be due to chance. Our negative results for these candidate regions have several possible explanations. First, the diagnostic criteria used in the previous studies ,10 that Previous studies attempting to confirm the high myopia loci on chromosomes 18 and 12 have yielded inconsistent results. Naiglin et al.collectedThese studies suggest that myopia is complex and probably caused by the interaction of multiple genes with the environment. Therefore, to understand myopia it is necessary to apply the equation: Genes + Environment=Outcome. The difficulty here is the uncertainty surrounding both terms in the equation; ideally, one set of genetic factors will interact with one set of environmental influences to produce identical outcomes, but it is unknown whether this is always going to be the case. Therefore, to lessen the problem of multiple gene interaction as well as gene-environment interaction confounding the results, strategies to limit this problem should be utilized in the genetic mapping of myopia. The use of isolated populations is one approach to limiting the heterogeneity across populations and is the approach we are using for a genome wide scan in these families. Furthermore, the definition of myopia needs to be standardized so comparisons across studies can be made accurately. Previous studies have utilized different requirements with regard to affection status making cross comparisons difficult. In conclusion, we find little evidence implicating previously described susceptibility loci for high myopia on chromosomes 12 and 18 as being important in the etiology of common, moderate/mild myopia in our two population samples.None declared.Dwight Stambolian, Lauren Reider, Debra Dana, Robert Owens, and Elise Ciner recruited patients for the study. Melissa Schlifka carried out the genotyping in chromosomes 18 and 12. Dwight Stambolian and Joan E. Bailey-Wilson performed the study design and wrote part of the manuscript. Joan Bailey-Wilson oversaw all statistical analyses; Grace Ibay performed statistical analyses and wrote part of the manuscript; Taura Holmes, Betty Doan and Jennifer O'Neill assisted with analyses of the data. All authors read and approved of the final manuscript.The pre-publication history for this paper can be accessed here:


The key to a rational treatment of elementary Mendelian genetics, specifically to an understanding of the origin of dominant and recessive traits, lies in the facts that: (1) alleles of genes encode polypeptides; (2) most polypeptides are catalysts, i.e. enzymes or translocators; (3) the molecular components of all traits in all cells are the products of systems of enzymes, i.e. of fluxing metabolic pathways; (4) any flux to the molecular components of a trait responds non-linearly (non-additively) to graded mutations in the activity of any one of the enzymes at a catalytic locus in a metabolic system; (5) as the flux responds to graded changes in the activity of an enzyme, the concentrations of the molecular components of a trait also change.It is then possible to account rationally, and without misrepresenting Mendel, for: the origin of dominant and recessive traits; the occurrence of Mendel's 3(dominant):1(recessive) trait ratio; deviations from this ratio; the absence of dominant and recessive traits in some circumstances, the occurrence of a blending of traits in others; the frequent occurrence of pleiotropy and epistasis. AA + 2Aa + aa) and the dominant, hybrid and recessive traits written as (AA + 2Aa + aa). This assumption  to call alleles dominant or recessive, and to represent them by the same letters used by Mendel to represent traits . on iunction" ).Beadle  expresseThis lack of attention to the implications of Garrod's work is all the more surprising when it is recalled that Bateson  indirectly by a system of enzymes  most of which, but not all, are enzymes . All polypeptides, catalytic and non-catalytic, are synthesised in this way.Figure X1, X2 and X3 in Figure X3 stands for those substrates that lead, through a series of enzyme-catalysed reactions, to the synthesis of nucleoside triphosphates (NTPs) and their subsequent incorporation into mRNA. Note that mRNA is a terminal product of this pathway. It is a coding entity, a proxy for DNA. Each mRNA specifies the order of incorporation of individual amino acids into a polypeptide, but no individual mRNA molecule participates as a substrate in the subsequent steps of the catalysed formation of a polypeptide. The control of the overall expression of a gene as a polypeptide is therefore necessarily treated in Metabolic Control Analysis as a cascade of two fluxing metabolic pathways, one that starts at X3, the other that starts at X2 [ts at X2 .X2 stands for those extracellular substrates that lead, through a series of enzyme-catalysed reactions, to the synthesis de novo of amino acids (AAs) and their subsequent incorporation, along with any existing amino acids, into a polypeptide (P). In a haploid cell, one polypeptide is synthesised from each gene locus. In a diploid, one polypeptide is synthesised from each of two alleles at a gene locus. If these pairs of polypeptides are catalytically active, each enzyme in a diploid cell  consists of a pair of allozymes, one of each pair specified by the allele derived from the male parent, the other specified by allele derived from the female parent. Each pair of allozymes, whether normal or mutated, exhibits only one measurable activity (v) at a catalytic locus in a metabolic pathway. If the pairs of polypeptides (P) synthesised by a diploid cell are not catalytically active they will not, of course, play a direct role in catalysing a metabolic pathway. They may have other important functions (e.g. as hormones) and may be components of traits.X1 stands for all those initial extracellular substrates feeding the matrix of inter-dependent biochemical pathways that typify all functioning cells. It is these pathways that generate the non-protein, non-polyribonucleotide, molecular products of all cell traits.Each of these three major fluxing pathways Figure  is catalX1 for the simple reason that this pathway stands for all the matrix of interdependent biochemical fluxes that generate such a wide range of the non-protein (and non-polyribonucleotide) molecular components of cell traits .Most attention is concentrated on the pathway initiated by X1.If any one of the three major pathways shown in Figure If the implications of the work of Beadle and Tatum  were notX1, X2, X3in Figure R) in permitting extracellular effectors to modulate intracellular metabolism (and thus the effects of a mutation) will be found elsewhere [Note that changes in the concentrations of external metabolites , the question then arises: how do we account for Mendelian segregation of traits during sexual reproduction? The answer lies in the fact that a mutation at a biochemical locus, within the matrix of interdependent pathways, has its most obvious effect on the most closely associated pathways. Distant pathways  will be less obviously affected. Kacser and Burns  The explanation advocated in this article for the origins of dominant and recessive traits from normal and mutant alleles in a diploid is based on:(i) An obligatory distinction, by notation and nomenclature, between the variables (traits) and the parameters  of genetic/biochemical systems.(ii) The contention that the molecular components of all traits are the products of fluxing metabolic systems Figures , 4, 5, 6(iii) Experimental evidence for an inevitable non-linear response of a flux (through a metabolic system of enzymes) to graded changes in the activity of any one of those enzymes , evidenc(iv) A demonstration that dominant and recessive traits arise from changes in the concentration of the normal molecular components of a defined trait.(v) The argument that changes in concentration of a trait component may nevertheless be revealed as a qualitative change in that trait.(vi) A demonstration that both alleles  at a locus in a diploid are generally expressed. If the normal allele expresses a catalytically active polypeptide, many mutants of this allele will express an enzyme with lower activity; a mutated enzyme with zero activity is an extreme case.uu, 2uU, UU) one of which is a unique heterozygote (uU).(vii) The demonstration that an explanation of Mendel's observations cannot be based on an allele series containing only three terms (e.g. (viii) A demonstration that dominant and recessive traits cannot be generated by those polypeptides that are not enzymes embedded in a system of enzymes.H) expresses a dominant trait (A) because the  recessive allele (u) in a heterozygote (Uu) is always completely ineffective or because the allegedly dominant allele (U) suppresses the allegedly recessive allele (u) in the heterozygote [(ix) Rejection of the unjustified traditional claim that a hybrid (rozygote .(x) Rejection of the traditional, unsubstantiated and implausible claim that one so-called dominant allele in a heterozygote is as effective as two such alleles in the wild-type cell .It was also shown that pleiotropy and epistasis can be explained by taking a similar system approach to that used in explaining the origin of dominant and recessive traits.It is then apparent that, to account rationally for Mendel's observations of dominant and recessive traits, a minimum of four conditions must be met.(i) Alleles must be distinguished by notation, nomenclature and concept from traits; functions of components of the genotype must be distinguished from properties of components of the phenotype. Traits alone may be dominant or recessive.(ii) Alleles cannot be called "dominant" or "recessive". .(iii) It must be shown how dominant traits become distinguishable from recessive traits in the same cell or organism Figure , 3.(iv) It must be shown how a hybrid trait sometimes becomes indistinguishable from the dominant trait and sometimes does not Figures , 3. The If all four conditions are be met; the first two conditions must first be met. The treatment given in sections 2–5 meets each of these requirements.origin of dominant and recessive traits that arose from mutations of alleles at any one gene locus in a diploid or polyploid cell . Inherent in this explanation, as set out above , are further explanations for the occurrence of the 3(dominant):1(recessive) trait ratio in some situations in a diploid  may produce a trait that is indistinguishable from the trait expressed from the "homozygous" allele pairs (UU).Kacser and Burns  providedsections .3, 2.4. In other words, provided:(a) all current misrepresentations of Mendel's paper  are firs(b) alleles are distinguished by notation and nomenclature from the traits they specify,(c) alleles are regarded as normal or mutant (but not dominant or recessive), it is possible to provide a rational and internally consistent explanation for the origin of Mendel's dominant and recessive traits, for the occurrence of his 3:1 trait ratio, and for exceptions to these observations noted by later investigators. The same systemic approach is applicable to current problems in biotechnology and medical genetics (section 4). It also explains the origins of pleiotropy and epistasis (section 5); and challenges the assumption that a mutation in a non-catalytic protein provides an example of Mendel's dominant and recessive traits [A + 2Aa + a). In the present paper these proportions have been written as (A + 2H + a). If the symbol (H) for a hybrid in Figure Aa), it will be clear why Mendel postulated that his hybrids (Aa) displayed trait (A) and not trait (a). If the same exercise is repeated in Figure H) temporarily by (Bb), it will be clear why Mendel observed an anomalous blending of flower colours in the hybrids when he crossed parental bean plants bearing different flower colours.Mendel found, by experiment, that the proportions of plant forms in each of his F2 populations was represented by  Persistent misrepresentations of Mendel's paper, and incorporation of these distortions into currently favoured explanations of Mendel's observations [ Persistespecify the kind (and order of incorporation) of amino acids into polypeptides . Dominance and recessivity are a reflection of changes in the concentration(s) of the molecular component(s) of a trait when an enzyme is mutated within a fluxing metabolic pathway.(2) A failure to recognise the consequences of not distinguishing between the function of the alleles and the properties of traits in attempting to explain Mendel's results. Normal and mutant alleles variables of a biological system to perturbations of the magnitude any one system parameter.(3) Tardy recognition of the need to adopt the systemic approach of Metabolic Control Analysis in explaining the response of the (4) A reluctance to accept a change in concepts even when currently accepted representations of Mendel's results are demonstrably untenable.(5) Elucidation of the double helical structure of DNA Figure  and all (6) A determination in some quarters to regard genetics as an autonomous subject. It has been obvious at least since the work of Beadle and Tatum  that sucIt is significant that Kacser & Burns were also one of two sets of authors who initiated the systemic approach to the control of metabolite concentrations and fluxes ,40. ThisA) and (a). These statements are here formally withdrawn. They were consistent with textbook treatments of Mendelian genetics [In an earlier paper  it was sgenetics  but a sugenetics  will be


Certain conditions characterised by blood vessel occlusion or vascular spasm have been found to cluster together in epidemiological studies. However the biological causes for these associations remain controversial. This study used a classical twin design to examine whether these conditions are linked through shared environmental exposures or by a common underlying genetic propensity to vasospasm.We investigated the association between hypertension, migraine, Raynaud's phenomenon and coronary artery disease in twins from a national register. Phenotype status was determined using a questionnaire and the genetic and environmental association between phenotypes was estimated through variance components analysis.Responses were obtained from 2,204 individuals comprising 525 monozygotic and 577 dizygotic pairs. There was a significant genetic contribution to all four traits with heritabilities ranging from 0.34 to 0.64. Multivariate model-fitting demonstrated that a single common genetic factor underlies the four conditions.We have confirmed an association between hypertension, migraine, Raynaud's phenomenon and coronary artery disease, and shown that a single genetic factor underlies them. The demonstration of a shared genetic factor explains the association between them and adds weight to the theory of an inherited predisposition to vasospasm. A number of conditions characterised by blood vessel occlusion and/or vascular spasm have been found to be associated in both clinical and epidemiological studies. These include hypertension (HPT), Raynaud's phenomenon (RP), migraine (MIG) and coronary artery disease (CAD) -5. WhethSubjects for this study were twins enlisted with the St Thomas' UK Adult Twin Registry . These mClassification of the traits HPT, RP, MIG and CAD was based on standard, validated criteria where possible. HPT was classified by asking about a doctor's diagnosis of "high blood pressure" when not pregnant. Questions to determine presence of migraine were based on the UCSD Migraine Questionnaire   corrected to take into account the paired nature of the data. The odds ratios were adjusted for possible confounding by age, smoking and body mass index (BMI). Evidence for a genetic contribution to each trait was examined by estimating casewise concordance . This meWhere data suggested a genetic influence, a quantitative measure of genetic contribution was estimated using structural equation modelling (Mx software ). This sModeling was then extended to consider the genetic and environmental associations between all four variables simultaneously . Three m1) the Cholesky decomposition  the independent pathway model  the common pathway model  with that of the fullest model, the Cholesky. The AIC represents the balance between model fit and the number of parameters (parsimony), with lower values of AIC indicating the most suitable model. Parameter estimates from the most appropriate model were used to calculate the genetic and environmental correlation between variables.Complete data for analysis were available from 1,102 pairs of female twins, comprising 525 MZ and 577 DZ pairs. The mean (± SD) age of the twins was 48.5 (± 8.2) years. The prevalence of each trait is shown in Table Four of the six combinations of traits showed significant phenotypic association after adjusting for age, smoking and BMI  declare that they have no competing interests.FMKW analysed the data and drafted the manuscript. LFC designed the questionnaires, analysed the data and assisted with the manuscript. TDS collected the twins on the Twin Register and assisted with the manuscript. AJM conceived of the study, collected the twins on the Twin Register, analysed the data and co-drafted the manuscript.The pre-publication history for this paper can be accessed here:


Locus heterogeneity poses a major difficulty in mapping genes that influence complex genetic traits. A widely used approach to deal with this problem involves modeling linkage data in terms of finite mixture distributions. In its simplest setup, also known as the admixture approach, a single parameter is used to model the probability that the disease-causing gene of a family is linked to a reference marker. This parameter is usually interpreted as the overall proportion of linked families.In this article, we address two issues regarding the admixture approach. First, we tackle the question of whether the single parameter of linked proportion is well defined in general. By formulating the likelihood under a classification scheme based on distributions, we show that such a parameter is meaningful only when a certain well-characterized condition is met. Second, we study a condition given in the literature for validating the admixture approach. A counter example is constructed to illustrate that the condition does not necessarily lead to valid estimates.Estimators from the admixture approach may be inconsistent. This holds even if a condition given in the literature to validate the approach is satisfied. The heterogeneity is modeled by a single parameter (α) that denotes the probability that a family is linked. This parameter is interpreted by many researchers as the overall proportion of linked families.Mapping disease genes influencing complex genetic traits is far more difficult than mapping genes underlying Mendelian traits. One of the difficulties is due to locus heterogeneity, in which the disease in different families  is caused by different loci or non-hereditary factors. Finite mixture distributions have been proposed to model linkage data in the presence of locus heterogeneity , also knα does not even measure the proportion of linked families within the sample, contrary to popular belief. Similar conclusions were obtained in the simulation study by Pal and Greenberg )n et al.  showed, In this article, we consider the same problems discussed in Janssen et al.  and WhitT types such that families in the same type follow the same distribution. That is, families are classified into the same type based on their "structures" that lead to the specification of their distributions. Here we use the term structure in a broad sense that includes not only the pedigree structure but also any other available information about the pedigree (such as knowledge of phase) that contributes to the distribution from which the family is generated. Note that structure does not include any phenotypic or genotypic data of a family. Families with the same structure but different phenotypic and/or genotypic data are simply different realizations from the same distribution and hence are iid, and are classified into the same type. In the most general setup, with g potential linkage scenarios, e.g., linked or unlinked (g = 2) in the simplest setting, the probability distribution, ft*, for a realization (yt) from type t, t = 1,…,T, can be expressed in terms of its component distributions, fti, i = 1,…,g [Suppose that data from independent families in the sample are classified into  = 1,…,g :αti ≤ 1 , , and θ is the linkage parameter vector, including various recombination fractions.where the mixing parameters satisfy 0 ≤ θ or by a locus unlinked to the reference marker. Further, we assume that the genetic (trait) models at the linked and unlinked loci are the same. So, the linkage parameter vector is θ = {θ, 1/2}, and the probability distribution is simplified toTo simplify our presentation without compromising our objectives, we assume that the disease under study is caused either by a locus linked to the reference marker with a recombination fraction ft* = αtft + (1 - αt)ft,αt is the probability that a type t family is linked. Note that the two distributions under the mixture have the same parametric form but differ in their linkage parameter values, being θ or 1/2. Also, note that a single α parameter is used for all families in the same type.where a denote the true proportion of linked families in the entire sample. Let pt, t = 1,…, T, be the true proportion of type t families in the linked group. Thus p =  is the distribution of types among the linked families. Recall that all families in a given type have the same distribution, i.e., same likelihood for any value of the recombination fraction. Similarly, define q =  to be the distribution of family types among the unlinked group. Then the probability that a family is of type t is st = apt + (1 - a)qt, and the probability that a type t family is linked is thus . Furthermore, let r denote the true common recombination fraction for the linked families. The likelihood contribution for estimating the parameters {αt, θ} by a type t family with data yt isLet Lt = αtft + (1 - αt)ft.     (1)t can be expressed asThen the expected contribution to the log-likelihood from a family of type r and  are the true underlying quantities, whereas θ and α =  are the parameters to be estimated from the data. Combining the expected log-likelihoods, ELLt, t = 1,…, T, we can form the total expected log-likelihood from all family types as follows:Note that α0, r) ≥ ELL, for any , following Stuart and Ord [α, θ). Note that α is a vector of nuisance parameters; only θ is the true parameter of interest.Since the above formulation of likelihood is correct under the stated assumptions, it can be shown that ELL families with the same structure (and hence their data coming from the same distribution as elucidated at the beginning of this section) share a common α parameter. Since the issue addressed by Vieland and Logue [We note that the above likelihood, although similar to the one presented in Vieland and Logue , is diffnd Logue  is diffep = q, that is, the distribution of family types among the linked families is the same as that among the unlinked families. In this setup, all αt's are set to be equal to a common parameter, α, the overall proportion of linked families. Hence, the total expected log-likelihood is with respect to the recombination fraction θ and a single proportion parameter α:In this subsection, we show that the two-parameter setup leads to correct likelihood formulation only when a, r) and , isThe expected log-likelihood ratio between the two sets of parameter values,  ≥ ELL, for any , implying that  = a and  = r are the maximum likelihood estimates of α and θ. However, as shown in the examples in the next section, when p ≠ q, ELL may be smaller than ELL for some parameter values . That is, the maximum likelihood estimates of α and θ may not be consistent because the likelihood model is incorrectly specified (under-parameterized). In order for the two-parameter formulation to be correct, the following constraints should be placed on the makeup of the families:In other words, when p = q given the additional constraints that  and . Notice that p = q is stronger than the LUFED condition. Equal distributions of types in the linked and unlinked families according to the classification scheme based on distributions of the data implies equal distributions of informativeness in the same two groups. Therefore, LUFED is a necessary condition for the admixture approach. We also note that p = q is not necessarily satisfied for every dataset (see Discussion).which implies that α, the relationship between α and αt is as follows:In general, in a parameterization that demands an estimate for the overall proportion of linked families, ut and vt are also unknown parameters (with constraints ∑ut = 1 and ∑vt = 1) that need to be estimated. Note that ut and vt are the parameters to be estimated from the data and are not necessarily the same as pt and qt, respectively, as the latter are the true values of the former. We have shown earlier that the maximum likelihood estimates for αt exist. However, one cannot solve the equations in (3) to obtain a corresponding estimate for α. This is because there are only T + 2 equations (including the two constraints) but 2T + 1 unknown parameters, and thus not all parameters are identifiable when T ≥ 2. Hence, one may not be able to find a meaningful estimate of the overall proportion of linked families, contrary to popular desire for such an estimate. This is consistent with the finding of Whittemore and Halpern [where  Halpern , althougWe have already shown that LUFED is a necessary condition for obtaining consistent estimators using the admixture approach. In this section, we investigate, through a contrived dataset, whether LUFED is also a sufficient condition for achieving satisfactory results, as contended by Janssen et al. . We use p1, and Phase Unknown (PU) families in proportion p2, where p1 + p2 = 1. The unlinked group is also composed of PK and PU families, but in proportions q1 and q2, respectively, where q1 + q2 = 1. We choose to work with the PK and PU families as the PK families were used by Janssen et al. [m children in all PK families and m + 1 children in all PU families. As these two types of families have different distributions [T = 2) under the classification scheme according to distributions.In our contrived dataset, the linked group consists of two types of families: Phase Known (PK) double backcross families in proportion n et al.  to evalum children is:Now, let us consider the ELOD of each family. The ELOD of a PK family with θ is the parameter for recombination fraction while r is the true recombination fraction. Similarly, one can find the ELOD of a PU family with m + 1 children:where, as before, r close to 0, it can be seen that ELODPK(θ) and ELODPU(θ) are both approximately m log10 2, when they are evaluated at θ = r [α parameters.For at θ = r  LUFED com/0, m - 1/1,..., 1/m - 1, 0/m) offspring.It is worth noting that this dataset may serve as an example for understanding classification based on distributions and family realizations that make up a family type. The phase information as well as the number of offspring are part of the family structure, which is the basis of classification according to distributions. However, phenotypes and genotypes do not configure into this classification scheme. For example, the PK data type consists of families with several phenotypes, i.e., various combinations of recombinant/non-recombinant , q = ; and (b) p = , q = . For each of these two settings, we take m = 3 children in PK families and m + 1 = 4 children in PU families. In both settings, the overall proportion of linked families, a, is 0.5, and the true  recombination fraction, r, is 0.02. So, as discussed above, the distribution of informativeness among the linked families, under the ELOD measure, is the same as that among the unlinked families. The two pictures in Figure α, θ) where the maximum expected log-likelihood occurs are not the same as their true values. So the estimates are inconsistent. The extent of this inconsistency depends on several factors, including how close p is to q. As seen in Figure p differs greatly from q, the parameter estimates are far away from the true values. On the other hand, in Figure p is close to q, the estimates are not too far from the truth. In fact, the estimates are expected to converge to the true parameter values when the difference between p and q approaches 0.To illustrate our results, we consider two specific settings for the distributions of families in the linked and unlinked groups under the classification scheme according to distributions: (a) = 0.9, 0., q =  in the two groups. Although the problem considered in Vieland and Logue [The first question of interest was addressed in Whittemore and Halpern , where tnd Logue  is diffeno under the ELOD measure for informativeness. The difference between the estimates and the true values of the parameters, even with infinite amount of data, can be large, if one would carry out the analysis under the admixture approach. This should serve as a warning against complacency when the LUFED condition is met. We do realize that, with phase known and phase unknown data, these examples can be quite extreme in human genetic studies, although such data arise frequently in experimental crosses. In situations where data from more general family structures are available, the effect of violation of the admixture approach assumptions may be much smaller.The second question stems from our curiosity on an argument made by Janssen et al.  for the The criteria for classification of families deserve further clarification because it is the heart of the problem. We discuss two criteria for classification, one according to the distributions of the data, and the other according to a measure of informativeness of the data for linkage studies (leading to the LUFED condition). The classification scheme based on the distribution criterion leads to a necessary and sufficient condition for validating the admixture approach. This result is a by-product of our theoretical development for finding an answer to the first question. The classification scheme based on the informativeness criterion, on the other hand, leads to the conclusion that LUFED is only a necessary, but not a sufficient, condition for the admixture approach, contrary to Janssen et al.'s  contentiFinally, we note that although the general formulation of likelihood based on forming groups of families with the same distribution gives consistent estimators, its practical utility seems to be limited. This is mainly due to the difficulty of classifying families according to distributions, in most applications, except for simple situations such as those involving only the PK and PU families. The general likelihood formulation is used here as a vehicle to further the understanding of potential problems in using the two-parameter admixture approach. A practical solution that embeds the correct likelihood formulation in a Bayesian framework is being pursued in a separate study.Both authors were involved in all aspects of this research project. Both authors read and approved the final manuscript.


Epidemiologic Perspectives & Innovations, provide a partial list of specific analyses and topic areas they would like to see submitted to the journal.As a supplement to our lead editorial, the editors of the new journal,  Epidemiologic Perspectives & Innovations (EP&I) present the underlying goals and philosophy of the journal, along with the types of articles we hope to publish. Here we clarify our goals with some specific ideas about articles we would like to see submitted to EP&I and with a "wish list" of methodological research and selected other innovations and perspectives we believe the field needs.In our lead editorial , the ediEP&I welcomes submissions of any papers in and of epidemiology, with the exception of those that solely report research results. "In and of" epidemiology includes papers about epidemiology and those grounded in other disciplines that might be useful for epidemiology. Many of our articles will be highly quantitative, but non-quantitative analyses are also welcome. We welcome submissions whose premises about how the field should be advancing differ from those of this editorial.This list is far from complete, and we want to emphasize that our intention is not to discourage submissions on topics not specifically mentioned here. EP&I hopes to help bridge the gap from best-practice methods to epidemiologic practice and teaching, and from there to epidemiology-based decision making.There is a gap between what methodologists know about doing epidemiology and standard epidemiologic practice. We believe that narrowing this gap is as important as the development of new methodological ideas. Papers that would narrow this gap are encouraged. These could take different forms, including: clear presentations of advanced methods that are underutilized , surveys of epidemiologic practice to assess where the gaps might be, papers that function as advanced textbook chapters, and teaching articles. We will give the highest priority to papers that achieve excellence in explanation.On a similar note, we would like to publish methods articles that fall into the category we call, "Don't Reinvent the Wheel." Other fields have different sets of methods that could be useful to epidemiologists, including observational methods from econometrics and related social sciences, uncertainty analysis methods from engineering and business, and historical perspectives from sciences with a longer history.Also on this theme, we plan to commission updates to classic methods papers from the original authors. Methodological knowledge is ever advancing, and it would be interesting and useful to see what changes an author would make to a must-read paper if that paper were written today. We welcome suggestions of candidates for this series.At the other end of the bridge, we invite methods and teaching papers that show how quantitative health researchers can present results that are more decision-relevant. We are especially interested in methods that go beyond statistical measures that emphasize merely whether an elevated risk has been found to ones that emphasize how much we ought to care about that elevated risk.EP&I have identified several specific methodological areas that we believe need attention. Without intending to restrict methodology submissions to these topics, we are particularly interested in submissions that deal with: (1) full and proper disclosure of uncertainty in study results, (2) decision-making in the face of this full disclosure, (3) identification and control of confounding, (4) quantifying the effect of random error on study results, and (5) specification error .The editors of Papers that fall into category (1) have begun to appear in the epidemiologic literature -11 but mWhile some fields have many papers that fall into category (2), including clinical decision making, there are very few in the epidemiologic literature.As a fundamental challenge for causal inference and a potential source of error in all observational study results, confounding is, and perhaps will always be, a thorn in the side of observational epidemiology . Papers Questions of how to think about, and quantify the effect of, random error in nonrandomized studies remain unresolved. A standard analysis pretends that researchers or nature randomized the study exposure to study subjects ,10. Is tStudy results are a function of both the data being analyzed and assumptions made in the process of the analysis -18. But EP&I. Epistemology in health science is often treated as a matter of statistical rules of thumb, with litigation serving as the ultimate arbiter. Neither statistical rules nor the results of lawsuits that go to trial are a particularly good source of knowledge.There is a substantial amount of epistemologic discussion in epidemiology, mostly relating to how we know if we are seeing a causal relationship and, to a lesser extent, what causation means. We hope that scientists in the field will become more actively engaged in practical epistemology , and we invite them to submit their work to Also falling under the broad category of philosophy is analysis of ethics. In the health sciences, such discussion is dominated by the issue of protecting human research subjects and patients. What is largely missing, and what we would like to invite submissions about, is the ethics of the core of our science: study design, data analysis, and result reporting. Since it is impossible to report every result that might be gleaned from a dataset, what constitutes an ethical choice of what to present? This question is central to most everything that most epidemiologists do, and yet there is remarkably little discussion about it . How manper se to include policy advocacy based on health science findings. Whether or not one takes that position, discussions of and about epidemiology should address questions of what society ought to do with our findings.  One interesting and timely set of questions involves the relative merits of decision-analysis or risk-analysis based decisions, "precautionary-principle" based decisions, and actual current practices.Many epidemiologists consider the field We seek to acknowledge the best epidemiologic studies and papers with articles that discuss what sets these studies apart from the rest: a "Best of Epidemiology" series. Much of methods training involves finding the worst in a study. We believe it would be useful to give students and other epidemiologists examples of how to do epidemiology well. What studies should we most want to emulate, and why?In a similar vein, we hope to receive submissions that remind us about the historical foundations of epidemiology: a "History of Epidemiology" series. What historical studies, insights, or methodology are important for understanding the field, and why, and which are simply interesting enough to be worth highlighting? History-of-science type analysis of our field, almost completely absent from the history-and-philosophy-of-science literature, would be particularly welcome.EP&I of such papers, whether or not a letter to the editor has been published. We encourage authors to take advantage of the speed of online publishing to submit re-analyses of important findings for publication while the implications of the original study are still being debated.  Readers of the health science literature may often find themselves asking a question about a study's results beyond the few specifically addressed in the published reports. A new analysis might be more relevant to a particular decision, or even out-and-out more informative than the original publication.A complement to the "best of" and recounting of historical high-points is reanalysis of particular study results or aspects of the field's literature more generally. Many substantive letters to the editor about published papers reflect a full article's worth of analysis by the letter authors. But those authors have little opportunity to publish that analysis, even when it has substantial practical or methodological importance; we encourage submission to EP&I article are encouraged to contact us in advance to see if we might solicit other related submissions to create a larger collection. Topics of particular interest to us, where we would like to encourage the starting of point-counterpoint series, include the usefulness of causal inference in epidemiology and the scientific basis for a particular regulatory decision . We especially encourage students to suggest potential topics.Finally, we hope to publish "Point-Counterpoint" collections on single topics. Authors considering writing a counterpoint (or simply a related point) to an We will grant that this is an ambitious research agenda. Perhaps it will be years before journals (this one or others) see articles on all these topics. But it is also possible that the next 100 dissertations in the field will include chapters that cover most of this ground. And perhaps those of us well past our dissertations can contribute a few also. We hope that asking (and providing a venue for publication) will make this much more likely.


The multiple metabolic syndrome is defined by a clustering of risk factors for cardiovascular disease. We sought to evaluate the familial correlations of the components of the syndrome using data from the Framingham Heart Study original and offspring cohorts as provided for the Genetic Analysis Workshop 13. Measures of plasma cholesterol , body mass index (BMI), and systolic blood pressure were used from selected calendar years of exams. Familial correlations were calculated using FCOR in S.A.G.E.The sibling correlations were relatively high for all measures and exams, from 0.17 for systolic blood pressure to 0.27 for HDL cholesterol. The parent-child correlations were very similar, except for systolic blood pressure. The avuncular correlations were much smaller and the cousin correlations were even smaller. For HDL cholesterol the avuncular correlation was half the sibling correlation and the cousin correlation was half that again. Spousal correlations ranged from 0.07 for systolic blood pressure to 0.34 for BMI. Correlations were somewhat lower from 1984 to 1987 examinations than from 1971 to 1975 examinations, except for spousal correlations for systolic blood pressure and BMI.The results of the family pair correlations are suggestive of genetic determinants of lipid levels and BMI. These components have been shown to be predictive of cardiovascular disease as well as diabetes. Genes in common with each of the components might also influence development of cardiovascular disease and diabetes, both complex diseases. The multiple metabolic syndrome, also known as syndrome X or the insulin resistance syndrome, is defined by a clustering of risk factors for cardiovascular disease. Although there is no common definition of the syndrome, it usually includes high plasma triglycerides, low HDL cholesterol, glucose intolerance, high blood pressure, obesity, and proteinuria . PersonsSome studies have begun to look at familial relationships of the syndrome. First-degree relatives of persons with diabetes are more likely to have the syndrome ,5. PersoData have been provided from the Framingham Heart study original and offspring cohorts. The Framingham Heart Study began in 1948 to study the risk factors and characteristics of cardiovascular disease. Adults between the ages of 28 and 62 years and living in Framingham, Massachusetts were recruited for the study. A total of 5209 people participated in the baseline examination and have been examined every two years since. Among these participants, several were identified as being biologically related or spouse pairs.To expand on the familial aspect of the study, the Framingham Offspring Cohort consisting of 3548 adult children of the original cohort and 1576 of their spouses were identified and recruited in 1971. This cohort has been followed roughly every four years (there were 8 years between the baseline and first follow-up exam). The protocols used were similar to the original Heart Study Cohort .The family relationships available within each cohort were limited. In the original cohort there were a number of sibling and spousal pairs, but very few multi-generational relationships (parent-child for example). Also, there were very few cousin relationships that had been identified. In the offspring cohort, again there were only sibling and spousal pairs available. Combining the cohorts provided the full range of family relationships. The family pedigrees were identified in the 1980s and 330 of the largest pedigrees have been provided in this data set. This consists of 3041 parent-offspring pairs, 2796 sibling pairs, 2107 avuncular pairs, 183 grandparent-grandchild pairs, and 1595 first-cousin pairs.For these analyses, we were interested in the continuous measurements that define the multiple metabolic syndrome. The relevant measures provided in the data set were: height and weight, HDL cholesterol and systolic blood pressure. Plasma triglycerides and glucose are important components of the multiple metabolic syndrome, but due to differences in collection between the cohorts, we only considered these measurements in the offspring cohort. Although both diastolic and systolic blood pressure would be of interest, only systolic was provided in the data set. Height and weight were not used individually, but were combined into body mass index (BMI) as a measure of obesity. BMI was calculated as weight (kg) divided by the square of the height (meters). We also used plasma total cholesterol since the HDL cholesterol was only measured at a few examinations.th, 15th, and 20th exams . The offspring cohort was first measured in 1971–1975 then again in 1979–1982 and every 4 years after that. The blood samples were 12-hour fasting samples. All factors of interest for this analysis were measured at each examination phase. Unknown differences in exam techniques between the cohorts may affect the multi-generational correlations.Each cohort had their own follow-up cycle and the measurements collected varied somewhat at each exam. The original cohort was first examined in 1948 and has had follow-up every 2 years. The blood samples were from non-fasting venous samples, so any measure of glucose or triglycerides provided will not be considered for analyses. Blood pressure and weight were available at each follow-up exam. Plasma total cholesterol was available at most examinations. Height was available consistently after 1972. HDL cholesterol was only provided for the 11th exam and in 1974 they were being seen for their 14th exam. To have one measurement for the original cohort during the years 1971 to 1975, we averaged all available measurements from the 13th and 14th exams.We selected examinations at a few points in time to examine correlations between pairs of relatives. We analyzed sibling correlations within each cohort separately for each of these times. We combined data from the two cohorts to maximally use the family relationships. Each examination phase for the offspring cohort encompassed two examination phases of the original cohort. In order to combine the cohorts, we averaged all available measurements for each cohort during specified calendar years. For example, from 1971 to 1975 the offspring cohort was being seen for their first exam. In 1972 the original cohort was being seen for their 13The first time chosen was 1968. At this time, only data from the original cohort were available (Exam 11). BMI was not available at this examination. The second time chosen was from 1971 to 1975. As described previously, the original cohort had participated in exams 13 and 14, from which measurements were averaged, while the offspring cohort had participated in their first exam. All measurements except HDL cholesterol were available for both cohorts. The third time chosen was from 1984 to 1987. During this time period, the original cohort had participated in Exams 19 and 20, from which measurements were averaged, while the offspring cohort had participated in Exam 3. All measurements were available for both cohorts at this time.Analyses were performed using FCOR (for correlations and their standard errors) in the S.A.G.E. package . Prior tThe mean of each measure and the mean age of participants at each examination by cohort is shown in Table Considering each examination and cohort separately, only sibling correlations were available Table . The corSince the correlations seemed fairly consistent, we combined the data as described in the Methods section. This provided sufficient numbers of pairs to estimate the parent-child, avuncular, and cousin correlations Table . For allThese data were supportive of a genetic component for HDL cholesterol and possibly for total cholesterol, BMI, and systolic blood pressure. For a trait whose variation is attributable entirely to additive genetic effects, the magnitude of the sibling and parent-child correlations should be similar, avuncular about half, and cousin correlations half again. Our sibling correlations were very close to the parent-child correlations for total plasma cholesterol, HDL cholesterol, and BMI. The avuncular and cousin correlations did drop by half for HDL cholesterol, but not for the other measures. These correlations were smaller than the sibling and parent-child correlations, however, and the cousin correlations were generally smaller than the avuncular correlations.For traits whose variation is attributable to genetic effects, spousal correlations should be 0. Many of the spousal correlations were significantly different from 0 and were similar in magnitude to the parent-child correlations. The spousal correlation for BMI in exams from 1984 to 1987 was nearly double the parent-child correlation. This was highly suggestive of an environmental influence on these traits. The spousal correlations were more variable between the exam phases, especially for systolic blood pressure and BMI. This may just be related to the smaller number of pairs available for spousal correlations. The environmental influence was also supported by higher sibling correlation than the parent-child correlation. These correlations may also have been affected by even small differences in examination procedures. The majority of the spousal pairs were all from the original cohort, while the sibling pairs included some pairs from the original cohort and some from the offspring cohort. The parent-child and avuncular correlations were all between pairs where one individual was in the original cohort and the other individual was in the offspring cohort.We observed a possible trend in decreasing correlations with time when considering the sibling correlations alone. In addition, we found the offspring cohort to have higher correlations than the original cohort, after adjusting for age. The decrease in correlation was very small, and likely not significant due to the wide confidence intervals. The decrease could be due to increasing variability in these measures that come with age or selective survival. Differences in morbidities within sibling pairs, causing a sibling to drop out of analyses, could affect the correlations. The spousal correlations were rather constant over time for plasma cholesterol and increased for BMI and systolic blood pressure.Family correlations of components of the multiple metabolic syndrome in the Framingham Heart Study and Offspring Study were consistent across outcomes and across cohorts. This was supportive of a genetic model to explain levels of these component characteristics. Segregation and linkage analyses may further our understanding of the genetic nature of each component. The clustering of these components has been shown to be predictive of cardiovascular disease as well as diabetes. Genes common to each of the components might also be responsible for these complex diseases.


Moreover, using average iteration and abundance scores for the 12 phenotypes and sex as their relevancy measurements, we found all relevant phenotypes for all four populations except phenotype b for the Karangar population, with suggested subgroup structure consistent with latent traits used in the model. In conclusion, our findings suggest that the ADTrees method may offer a more accurate representation of the disease status that allows for better detection of linkage evidence.We applied the alternating decision trees (ADTrees) method to the last 3 replicates from the Aipotu, Danacca, Karangar, and NYC populations in the Problem 2 simulated Genetic Analysis Workshop dataset. Using information from the 12 binary phenotypes and sex as input and Kofendrerd Personality Disorder disease status as the outcome of ADTrees-based classifiers, we obtained a new quantitative trait based on average prediction scores, which was then used for genome-wide quantitative trait linkage (QTL) analysis. ADTrees are machine learning methods that combine boosting and decision trees algorithms to generate smaller and easier-to-interpret classification rules. In this application, we compared four modeling strategies from the combinations of two boosting iterations  coupled with two choices of tree generation types . These four different strategies were applied to the founders in each population to construct four classifiers, which were then applied to each study participant. To compute average prediction score for each subject with a specific trait profile, such a process was repeated with 10 runs of 10-fold cross validation, and standardized prediction scores obtained from the 10 runs were averaged and used in subsequent expectation-maximization Haseman-Elston QTL analyses (implemented in GENEHUNTER) with the approximate 900 SNPs in Hardy-Weinberg equilibrium provided for each population. Our QTL analyses on the basis of four models  detected evidence for linkage (Z ≥ 1.96,  Alternating decision trees (ADTrees) are machine learning methods combining boosting and decision trees algorithms to generate classification rules . TraditiADTrees, a natural extension of both voted-stumps and decision trees, consist of alternating layers of prediction and decision nodes . The strt, a decision node, together with its two prediction nodes, is introduced. For full ADTrees, the decision node may be attached to any previous prediction node, leaf nodes or otherwise, including the root prediction node. Each prediction node is associated with a weight, α, which represents its contribution to the final prediction score, F(x), for every path that reaches it. Hence the contribution of each decision node may be understood in isolation, and summing the individual contribution gives rise to the final prediction and classification.Boosting is a general and effective method of combining moderately successful rules to produce very accurate prediction. As outlined in Figure In this study, we present the results of ADTrees in conjunction with genome-wide quantitative trait linkage (QTL) scans. Three quantitative measurements, including prediction, iteration, and abundance scores, were obtained from the ADTree-based classifiers using information from the 12 phenotypes and sex. With the help of the quantitative information, we aimed to gain a better understanding of the relationship between disease phenotypes and affection status as well as the risk profiles for each individual. The prediction scores, serving as a composite view of disease status, were then used to carry out genome-scan linkage analysis.The Problem 2 simulated data were used in this study and all analyses were performed without knowledge of the answers except the final comparison with disease models and regions of real linkage. The datasets comprised four populations, Aipotu, Danacca, Karangar, and NYC. Within each population, we arbitrarily selected the last three replicates out of the total 100 replicates available to the Genetic Analysis Workshop 14 (GAW14) participants.We used ADTrees decision-trees with AdaBoost boosting algorithm implemented in MLJAVA  to constWe chose founders in each population to construct the classifiers. The classifiers for each population were trained and tested by a total of 10 runs of 10-fold cross validation. Within each run, one-tenth of the founders in each population were reserved as a test set and the rest were used as a training set.The prediction score of disease status for each individual was derived directly from the ADTree model. Figure The iteration score and abundance score were additional quantitative measurements estimated from the individual tree structure associated with a classifier built during each run . The numThe prediction scores were used as a quantitative trait for QTL analysis in four populations using 917 single-nucleotide polymorphism (SNP) genotypes in the last 3 replicates. Prior to the analysis, Hardy-Weinberg equilibrium (HWE) tests of each population were first carried out using founder genotype information. Around 900 SNPs in HWE  were then retained for further analyses. Four genome scans for each population were performed using prediction scores computed from four different classification models; that is, full-ADT or BDT tree models paired with either exponential or log loss function. The expectation-maximization Haseman-Elston (EM-HE) method as implemented in GENEHUNTER [In all four populations, the average size of iteration steps over 10 runs of 10-fold cross validation during the boosting appeared to be the smallest in the full-ADT and largest in the BDT classifiers, suggesting that the full-ADT classifier performed better than the BDT. Although the log loss function appeared to perform slightly better than the exponential loss function except in the Karangar population, the two loss functions only differed by one step. The average size of all four classification models in all four populations is presented in Table Full-ADT with either exponential or log loss function extracted all relevant phenotypes used in the disease simulation models for all four populations without any false positive through either iteration or abundance scores averaged over 10 runs of 10-fold cross validation, as shown in Table Furthermore, iteration scores of relevant phenotypes from full-ADT suggested certain grouping structures, as shown in Table p < 0.01) on chromosomes 1, 3, 5, and 9, where SNP markers were closest to disease-related loci, as shown in Table Using average prediction scores from full-ADT as a quantitative trait for QTL analysis, with either exponential or log loss function then averaged over 10 runs of 10-fold cross validation, our genome scans attained significant evidence of linkage (Z ≥ 1.96, In this study, we applied the ADTrees method to the Problem 2 dataset and generated a new quantitative trait for each individual based on average prediction scores using information from the 12 phenotypes and sex. In short, the full-ADT approach performed better than BDT, while the exponential and logarithmic loss functions provided essentially comparable results. Using average iteration and abundance scores for the 12 phenotypes and sex, full-ADT extracted all relevant phenotypes without any false positive for all four populations except phenotype b for the Karangar population. Furthermore, iteration scores of relevant phenotypes from full-ADT suggested a subgroup structure consistent with latent traits used in the model. The order of relevant phenotypes by average iteration and abundance scores also indicated that the four populations were quite different from one another. In the QTL analyses, these methods identified significant evidence of linkage where SNP markers were closest to disease-related loci. SNP markers with false-negative and false-positive evidence of linkage were also considered. Future QTL analysis in combination with iteration scores and abundance scores may yield even better results than traditional qualitative trait linkage through a summary of relevant traits that contribute to disease status. In summary, our findings suggest that the ADTrees method is feasible and offers the advantage of a more accurate representation of the disease status.ADTrees: Alternating decision treesBDT: Boosting decision treeEM-HE: Expectation-maximization Haseman-ElstonGAW14: Genetic Analysis Workshop 14HWE: Hardy-Weinberg equilibriumQTL: Quantitative trait linkageSNP: Single-nucleotide polymorphismK-YL conceived of the study, participated in its design, carried out ADTrees analyses, and drafted the manuscript. JL participated in its design, and carried out QTL linkage analyses. XZ was responsible for the background in machine learning methodology. STCW participated in the design of the study. All authors read and approved the final manuscript.