Being a morning person is a behavioural indicator of a person’s underlying circadian rhythm. Using genome-wide data from 697,828 UK Biobank and 23andMe participants we increase the number of genetic loci associated with being a morning person from 24 to 351. Using data from 85,760 individuals with activity-monitor derived measures of sleep timing we find that the chronotype loci associate with sleep timing: the mean sleep timing of the 5% of individuals carrying the most morningness alleles is 25 min earlier than the 5% carrying the fewest. The loci are enriched for genes involved in circadian regulation, cAMP, glutamate and insulin signalling pathways, and those expressed in the retina, hindbrain, hypothalamus, and pituitary. Using Mendelian Randomisation, we show that being a morning person is causally associated with better mental health but does not affect BMI or risk of Type 2 diabetes. This study offers insights into circadian biology and its links to disease in humans. GWAS have previously found 24 genomic loci associated with chronotype, an individual’s preference for early or late sleep timing. Here, the authors identify 327 additional loci in a sample of 697,828 individuals and further explore the relationships of chronotype with metabolic and psychiatric diseases. Chronotype, often referred to as circadian preference, describes an individual’s proclivity for earlier or later sleep timing and is a physical and behavioural manifestation of the coupling between internal circadian cycles and the need for sleep, driven by sleep homoeostasis. Significant natural variation exists amongst the human population with chronotype typically measured on a continuous scale2, though individuals are often separated into morning people (or “larks”) who prefer going to bed and waking earlier, evening people (or “owls”) who prefer a later bedtime and later rising time, and intermediates who lie between the two extremes4. Age and gender as well as environmental light levels explain a substantial proportion of variation in chronotype, but genetic variation is also an important contributor8.Circadian rhythms are fundamental cyclical processes that occur in most living organisms, including humans. These daily cycles affect a wide range of molecular and behavioural processes, such as hormone levels, core body temperature and sleep–wake patterns10. Animal model studies have shown that mutations in, and altered expression of, key circadian rhythm genes can cause obesity, hyperglycaemia and defective beta-cell function leading to diabetes13. In humans, there are many reported associations between disrupted circadian rhythms and disease15, but the evidence for a causal role of chronotype on disease is limited16. For example, evening people have an increased frequency of obesity17, Type 2 diabetes18 and depression19 independent of sleep disturbance, and studies of shift workers show an increased risk of diabetes, depression and other diseases20. However, these associations could be explained by reverse causality (diseases affecting sleep patterns or dictating job options) or confounding (common risk factors influencing both chronotype and disease). Genetic analyses identifying variants robustly associated with putative risk factors, such as chronotype, can improve causal understanding by providing genetic instruments for use in Mendelian Randomisation (MR) analyses23, which minimise the effect of both reverse causality and bias caused by confounding. Identifying genetic variants associated with chronotype and sleep timing will also provide insights into the biological processes underlying circadian rhythms and sleep homoeostasis.There is evidence that alterations to circadian timing are linked to disease development, particularly metabolic and psychiatric disorders26, using a maximum of 128,286 individuals, identified a total of 24 independent variants associated with self-report chronotype. In this study, we perform a GWAS meta-analysis of a substantially expanded set of 697,828 individuals, including 248,098 participants from 23andMe Inc., a personal genetics company, and 449,734 participants from UK Biobank28. In addition to confirming an enrichment of circadian rhythm and brain expressed genes at chronotype-associated loci and genetic correlation with mental health disorders26, we identify 327 additional chronotype-associated loci and demonstrate that the chronotype-associated variants are associated with objective measures of sleep timing, but not sleep duration or quality, in 85,760 UK Biobank participants. By fine-mapping the genetic associations at all loci, we identify 10 coding variants with a high likelihood of being the causal variant, providing prospective targets for chronobiological investigation and go on to show evidence of a causal link between chronotype and mental health by MR.Three previous genome-wide association studies (GWAS)P < 5 × 10−8, of which 258 reached P < 6 × 10−9, a correction for the significance threshold based on permutation testing  = 0.5%), previously reported to be a monogenic cause of familial advanced sleep phase syndrome29, were associated with self-reported morningness (odds ratio (OR) = 1.44 for minor allele; P = 2 × 10−38) but with a lower magnitude of effect on sleep timing than expected in the activity-monitor derived measures of chronotype, advancing sleep timing (as measured by time of minimum activity) by only 8 min : 4–13, P = 4.3 × 10−4) as opposed to the average 4.2 h reported in the previous study29.Well-documented circadian rhythm genes were among the most strongly associated loci  and midpoint of the most-active 10 h of the day (M10 timing). Summary statistics of these derived phenotypes and their associations with self-report morningness are presented in Supplementary Table P < 5 × 10−8 from this meta-analysis that were available in the UK Biobank imputed genotype data, 258 had a consistent direction of effect for sleep midpoint , 262 with L5 timing  and 260 with M10 timing . A genetic risk score (GRS) of these 292 variants was associated with earlier sleep midpoint, L5 timing and M10 timing . There was little evidence of association between the chronotype GRS and the activity monitor sleep phenotypes that estimate sleep duration and fragmentation  nervous system and brain development, components of neuronal cells such as synapses, axons and dendrites, as well as neurogenesis. There was clear enrichment in all types of brain tissue  patterns and outputs the posterior probabilities of each variant configuration being causal. Forty-two loci had a single variant with a probability of >50% of being causal , previously associated with chronotype25 and the most strongly associated with morningness in this study, and missense variants in the INADL, HCRTR2, PLCL1 and CLN5 genes, all four genes having been identified in previous GWAS26. Fine-mapping also identified missense variants in PCYOX1 and SKOR2, and a stop gain variant in the MADD gene, as likely causal variants in these loci, highlighting further candidate genes for chronotype. The MADD stop gain variant (rs35233100) has previously been associated with levels of proinsulin42, suggesting a potential link between insulin secretion and chronotype. To gain further insight into additional genes that may play a role in determining chronotype, we annotated the putative causal variants using the GTEx eQTL database ubiquitination has been shown to be involved with the degradation of several core clock genes44, influencing the build-up up these proteins and the pace of the circadian clock46. FBXO3 expression has been shown to be altered by light treatment and to demonstrate rhythmic expression46.To highlight putative causal variants and genes, we fine-mapped the associated loci using FINEMAPPER1, PER2, PER3, CRY1, FBXL3 and ARNTL  were enriched in the SCN, representing a significant excess . As a negative control, we tested the enrichment of MAGMA-mapped genes for several unrelated GWAS phenotypes, finding no significant excess of SCN-enriched genes   is a small region of the brain, consisting of around 20,000 neurons, that is integral to maintaining circadian rhythms in humans and is a likely mechanism of action for at least some of the associated genes and loci. Indeed, the associated loci included many key mammal SCN clock genes including 53, and to identify genetic overlap between chronotype and other diseases and traits, we performed LD-score regression analyses against a range of other diseases and traits for which GWAS summary statistics were publicly available . Psychiatric traits schizophrenia , depressive symptoms , major depressive disorder  and intelligence  were all negatively correlated with the morning chronotype. Metabolic traits fasting insulin  and HOMA-IR  were negatively correlated with being a morning person but did not reach our Bonferroni-corrected significance threshold. Body mass index (BMI)  and T2D  were not genetically correlated with morningness.As a strategy to prioritise traits for subsequent causal analyses, as previous studies have shown a strong correlation between genetic and phenotypic correlationsFTO (rs1558902) previously associated with higher BMI55 was also associated with being a morning person , we also performed two-sample MR against the metabolic phenotypes BMI, type 2 diabetes and fasting insulin levels. For individual instrument effects on chronotype, log ORs (representing liability for morningness) from the secondary morning person meta-analysis were used, as no effect sizes were obtained in the primary meta-analysis. With chronotype as an exposure, we implemented the R package TwoSampleMR56 to report causal associations of chronotype on these eight outcomes (Supplementary Data P = 0.004) and higher subjective well-being (0.04 SD (0.02–0.06); IVW P = 5 × 10−5), and with good agreement amongst the different MR methods  for major depressive disorder and 0.02 SD lower  for depressive symptoms , as previously reported26.Genetic correlations do not allow for statements of causality to be made about the association between an exposure and an outcome. We therefore performed two-sample MR analyses against the five psychiatric traits that showed evidence of a genetic correlation, to estimate causal effects. Because of the extensive literature on the link between chronotype and metabolic disease and because the well-known SNP in FTO rs158902 preP = 0.01), insulin secretion (IVW P = 0.04) and BMI (IVW P = 0.05) on chronotype. Despite strong genetic correlations with chronotype, we see no strong evidence that schizophrenia (IVW P = 0.07) or major depressive disorder (IVW P = 0.62) causally influence liability for morningness.To assess whether our genetically correlated phenotypes were causally influencing chronotype, we performed two-sample MR analyses with chronotype as the outcome. Owing to a limited number of genetic instruments, of the original five genetically correlated psychiatric phenotypes we were able to test only schizophrenia and major depressive disorder, in addition to the metabolic phenotypes BMI, insulin secretion and type 2 diabetes , we infer that some of the variation is attributed to subtle differences in the biochemical feedback mechanism of the circadian clock. This is supported by evidence of the chronotype-associated loci being enriched in the SCN, suggesting that variants that also subtly affect the modification and regulation of the circadian clock contribute to the population variation of chronotype. Entrainment of circadian rhythms through external stimuli such as light and temperature is well-known but through this study and previous GWAS efforts, we found that an individual’s chronotype is also influenced by variants in genes important in the correct formation and functioning of retinal ganglion cells (RGS16 and INADL), highlighting that some natural variation could be explained by better detection and communication (to the SCN) of external light signals. Variants in genes with known roles in appetite regulation (FTO), insulin secretion (MADD) and even nicotine and caffeine metabolism (CYP2A6) point to other processes that impact an individual’s chronotype, though it is unclear whether the effect of these on chronotype are mediated through the modulation of the circadian clock or by other means, such as through sleep–wake homoeostasis.We have found evidence that the natural variation in circadian preference amongst the human population can be ascribed to several different mechanisms. Given the prominence of genetic variants in or near multiple core circadian rhythm genes  and RELN40 and subsequent studies will be necessary to understand the shared biological mechanisms between chronotype and schizophrenia risk.There are clear epidemiological associations reported in the literature between mental health traits and chronotype, with mental health disorders typically being overrepresented in evening typesChronotype is influenced by circadian rhythms and innate sleep homoeostatic mechanisms, but is also dependent on societal pressures. It is also a self-report measure which means the interpretation of the phenotype and the genetic association is complicated. In this study, however, we show, using objective measures derived from activity monitor data, that these chronotype variants do affect objectives measures of sleep timing, but not other aspects of sleep including duration and timing, providing evidence that we are identifying biologically meaningful associations and allowing us to quantity the effect of these variants on sleep timing.64. Here, GWAS results replicated those of 23andMe, a study that may also suffer from selection bias but of a different nature to UK Biobank. Adopting two-sample MR we attempted to maximise statistical power by using publicly available aggregated data based on consortia of studies that had considerably greater response rates, and avoided winner’s curse which can lead to underestimation of causal effects65. MR of a binary (or other broad category) exposure that is derived from an underlying continuous trait, as is the case with chronotype, may be biased by horizontal pleiotropy from within-category variation in the trait that cannot be identified by alternative MR methods, such as MR-Egger. As effect sizes for MR analyses were derived from log ORs in the secondary morning person meta-analysis, there may be the possibility of undetected pleiotropy and so our findings should therefore be treated with some caution.The response to UK Biobank participation was <5% and this has resulted in selection for healthier individuals, which may introduced bias into our analyses, including in GWAS and MRIn conclusion, we have identified 327 novel loci that regulate circadian rhythms and sleep timing in humans and provide further insights into the association of chronotype with disease.http://www.ukbiobank.ac.uk/ethics/) and covers the work in this study, which was performed under UK Biobank application number 9072. All participants included in these analyses gave informed consent to participate. UK Biobank consent procedures are detailed at http://biobank.ctsu.ox.ac.uk/crystal/field.cgi?id=200. All 23andMe participants were customers of the personal genetics company 23andMe, Inc. and were genotyped for the 23andMe Personal Genome Service. The 23andMe participants included in our analyses provided informed consent for their data to be used for research purposes and responded to online questionnaires according to 23andMe’s human subject protocol, which was reviewed and approved by Ethical and Independent Review Services, a private institutional review board (http://www.eandireview.com). Details of 23andMe’s consent process can be found at https://www.23andme.com/en-gb/about/consent/.The UK Biobank was granted ethical approval by the North West Multi-centre Research Ethics Committee (MREC) to collect and distribute data and samples from the participants  reference panel using a subset of variants that were of a high quality in the UK Biobank. We projected these principal components into the set of related UK Biobank participants to avoid the relatedness confounding the principal components. We then adopted a k-means clustering approach to define a European cluster, initialising the ethnic centres defined by the population-specific means of the first four 1KG principal components. This analysis was performed only within individuals self-reporting as British, Irish, White or Any other white background. Because association analyses are performed using the LMM method, we included related individuals.The UK Biobank is a health resource with phenotypic and genetic data on over 500,000 volunteer participants who were aged between 40 and 69. Participants were recruited from the general UK population and baseline data were collected from 2006 to 2010 across 22 centres in England, Scotland and Wales, with recording of detailed anthropometric measures as well as self-report health and sociodemographic variables. The cohort is described in full elsewhere24.We used summary statistics from a morning chronotype GWAS performed by 23andMe of 248,100 participants  with a minimum of 97% European-ancestry. GWAS analysis was performed in a maximal set of unrelated participants, where pairs of individuals were considered related if they shared 700 cM IBD of genomic segments, roughly corresponding to first cousins in an outbred population. The 23andMe cohort is described in more detail elsewhere66. Detailed protocol information can be found online at http://biobank.ctsu.ox.ac.uk/crystal/docs/PhysicalActivityMonitor.pdf and a sample instruction letter at http://biobank.ctsu.ox.ac.uk/crystal/images/activity_invite.png . We converted the .cwa files to .wav format using the open-source software omconvert, recommended by the activity monitor manufacturers Axivity, which is available online . To process the raw accelerometer data in.wav format, we used the freely available R package GGIR (v1.5-12)68. The list of our GGIR settings is provided in Supplementary Data https://cran.r-project.org/web/packages/GGIR/GGIR.pdf).A subset of the UK Biobank cohort was invited to wear a wrist-worn activity monitor for a period of a week. Individuals were mailed the device and asked to wear it continuously for seven days, including while bathing, showering and sleeping. In total, 103,720 participants returned their activity monitor devices with data covering at least three complete 24-hour periods. We downloaded the raw activity monitor data (data-field 90001) for these individuals, in the form of binary Continuous Wave Accelerometer (cwa) files. Further information, along with details of centrally derived variables, is available elsewherer2 ≥ 0.3, MAF ≥ 0.001 (0.1%) and that showed no sign of batch effects.The 23andMe cohort was genotyped on one of four custom arrays: the first two were variants of the Illumina HumanHap550 + BeadChip (4966 cases and 5564 controls), the third a variant of the Illumina OmniExpress + BeadChip  and the fourth a fully custom array . Successive arrays contained substantial overlap with previous chips. These genotypes were imputed to ~15.6 million variants using the September 2013 release of the 1000 Genomes phase 1 reference panel. For analyses, we used ~11.9 million imputed variants with imputation r2 ≥ 0.3, MAF ≥ 0.001 (0.1%) and with a Hardy–Weinberg equilibrium (HWE) P > 1 × 10−12 . We excluded non-HRC imputed variants on advice from the UK Biobank imputation team. Further details on the UK Biobank genotyping, quality control and imputation procedures can be found elsewhere28.The UK Biobank cohort was genotyped on two almost identical arrays. The first ~50,000 samples were genotyped on the UK BiLEVE array and the remaining ~450,000 samples were genotyped on the UK Biobank Axiom array in two groups (interim and full release). A total of 805,426 directly genotyped variants were made available in the full release. These variants were centrally imputed to ~93 M autosomal variants using two reference panels: a combined UK10K and 1000 Genomes panel and the Haplotype Reference Consortium (HRC) panel. For all analyses, we used ~12.0 M HRC imputed variants with an imputation N = 120,478) and evening people were coded as 0 .Responses to two identical questions  were used to define the dichotomous morning person phenotype in the 23andMe cohort, with one question having a wider selection of neutral options. For the first instance, the possible answers were “Night owl”, “Early bird” and “Neither”, and for the second “Night person”, “Morning person”, “Neither”, “It depends” and “I’m not sure”. Individuals with discordant or neutral responses to both were excluded. For those with one neutral and one non-neutral response, their non-neutral response was used to define their phenotype. Morning people were coded as 1 ”; data-field 1180). Participants were prompted to answer the question “Do you consider yourself to be?” with one of six possible answers: “Definitely a ‘morning’ person”, “More a ‘morning’ than ‘evening’ person”, “More an ‘evening’ than a ‘morning’ person”, “Definitely an ‘evening’ person”, “Do not know” or “Prefer not to answer”, which we coded as 2, 1, −1, −2, 0 and missing, respectively  and those answering “Definitely a ‘morning’ person” and “More a ‘morning’ than ‘evening’ person” were coded as 1 (cases). Participants answering “Do not know” or “Prefer not to answer” were coded as missing. A total of 403,195 participants were included in the GWAS .69 produces quantitative and timing measures relating to both activity levels and sleep patterns, with a day-by-day breakdown, as well averages across the period of wear. A new algorithm, implemented in version 1.5–12 of the GGIR R package and validated using PSG in an external cohort70, allows for detection of sleep periods without the use of a sleep diary and with minimal bias. Briefly, for each individual, median values of the absolute change in z-angle  across 5-min rolling windows were calculated across a 24-h period, chosen to make the algorithm insensitive to activity monitor orientation. The 10th percentile was incorporated into the threshold to distinguish movement from non-movement. Bouts of inactivity lasting ≥30 min are recorded as inactivity bouts. Inactivity bouts that were <60 min apart were combined to form inactivity blocks. The start and end of longest block defined the start and end of the sleep period time-window (SPT-window).The software package GGIR3 + 1.5 × IQR) or a non-zero count of “interrupted recording periods” (field 90180). Phenotypes determined using the SPT-window  had additional exclusions based on short (<3 h) and long (>12 h) mean sleep duration and too low (<5) or too high (>30) mean number of sleep episodes per night (see below). These additional exclusions were to ensure that individuals with extreme (outlying), and likely incorrect, sleep characteristics were not included in any subsequent analyses.The UK Biobank made multiple activity monitor data-quality variables available. From our activity monitor phenotypes, we excluded 4925 samples with a non-zero or missing value in data-field 90002 (“Data problem indicator”). We then excluded any individuals with the “good wear time” flag (field 90015) set to 0 (No), “good calibration” flag (field 90016) set to 0 (No), “calibrated on own data” flag (field 90017) set to 0 (No), “data recording errors” (field 90182) > 788  with a cut-off at midday (12:00 and 36:00). This accounted for participants whose sleep midpoint occurs before midnight. Our sleep midpoint phenotype represented the average of each participant over all their valid SPT-windows. After exclusions and adjustments, 84,810 participants had valid sleep midpoint, covariates and genetic data.L5 and M10 refer to the least-active five and the most-active 10 h of each day and are commonly studied measures relating to circadian activity and sleep. L5 (M10) defines a 5-h (10-h) daily period of minimum (maximum) activity, as calculated by means of a moving average with a 5-h (10-h) window. As with sleep midpoint, we defined our L5 (M10) timing phenotype as the number of hours elapsed from the previous midnight to the L5 (M10) midpoint, averaged over all valid wear days. Of the 103,711 participants with activity monitor data, there were 85,205 and 85,670 with valid L5 and M10 timing measures respectively, covariates and genetic data. Basic summaries of these and other raw activity monitor phenotypes are given in Supplementary Table z-axis of the activity monitor68. The summed duration of all sleep episodes provided the sleep duration for a given SPT-window. We took both the mean and standard deviation of sleep duration across all valid SPT-windows to provide a measure of average sleep quantity and a measure of variability. After exclusions and adjustments, we had 85,449  participants with valid sleep duration mean (SD), covariates and genetic data.Sleep episodes within the SPT-window were defined as periods of at least 5 min with no change larger than 5° associated with the Sleep efficiency was calculated as a ratio of sleep duration (defined above) to SPT-window duration. The phenotype represented the mean across all valid SPT-windows and after exclusions and adjustments, left us with 84,810 participants with valid sleep efficiency, covariates and genetic data.The number of sleep episodes was defined as the number of sleep episodes of at least 5 min separated by at least 5 s of wakefulness within the SPT-window. The phenotype represented the mean across all SPT-windows and, once adjusted for the mean length of time in bed, can be interpreted as a measure of sleep disturbance or fragmentation. After exclusions and adjustments, we had 84,810 participants with a valid number of sleep episodes, covariates and genetic data.Diurnal inactivity was defined as the total daily duration of estimated bouts of inactivity that fall outside of the SPT-window. This comprised the total length of periods of sustained inactivity (>5 min) and captured sleep (naps), but did not include other inactivity such as sitting and reading or watching television, which involve a low but detectable level of movement. This variable likely captured some non-sleep rest as it was not possible to separate these without detailed activity diaries. The phenotype was calculated as the mean across all valid days and, after exclusions and adjustments, we were left with 84,757 participants with a valid measure, covariates and genetic data.71 v2.3, which applies a linear mixed model (LMM) to adjust for the effects of population structure and individual relatedness, and allowed us to include all related individuals in our white European subset, boosting our power to detect associations. This meant a sample size of up to 449,734 individuals, as opposed to the set of 379,768 unrelated individuals. BOLT-LMM approximates relatedness within a cohort by using LD blocks and avoids the requirement of building a genetic-relationship matrix, with which calculations are intractable in cohorts of this size. From the ~805,000 directly genotyped (non-imputed) variants available, we identified 524,307 high-quality variants  that BOLT-LMM used to build its relatedness model. For LD structure information, we used the default 1000 Genomes LD-Score table provided with the software. We forced BOLT-LMM to apply a non-infinitesimal model, which provides better effect size estimates for variants with moderate to large effect sizes, in exchange for increased computing time. At runtime, the chronotype and morning person phenotypes were adjusted for age (field 21003), sex (field 31), study centre  and a derived variable representing genotyping release . Accelerometer-based phenotypes were adjusted at runtime for age activity monitor worn (derived from month and year of birth and date activity monitor worn), sex, season activity monitor worn  and number of valid measurements . The GWA analysis for the number of sleep episodes phenotype was also adjusted for the mean length of SPT-window  to account for the fact that individuals have a greater number of sleep episodes the longer they spend in bed.We performed all association test using BOLT-LMMλGC of 1.325 was reported for this GWAS. Lead variants for the 23andMe only morning person GWAS are provided in Supplementary Data In the 23andMe morning person GWAS, the summary statistics were generated through logistic regression (using an additive model) of the phenotype against the genotype, adjusting for age, sex, the first four principal components and a categorical variable representing genotyping platform. Genotyping batches in which particular variants failed to meet minimum quality control were not included in association testing for those variants, resulting in a range of sample sizes over the whole set of results. A To avoid issues with stratification, we performed a sensitivity GWAS, in UK Biobank alone, to assess whether any of the associations were driven by a subset of the cohort with specific conditions. We excluded those reporting shift or night shift work at baseline, those taking medication for sleep or psychiatric disorders and those with either with a HES ICD10 or self-reported diagnosis of depression, schizophrenia, bipolar disorder, anxiety disorders or mood disorder , calculated by the software LDSC, as using λGC is considered overly conservative and the LD-score intercept better captures inflation due to population stratification74. For interpretable results, we reported the OR from a secondary effect size meta-analysis between our dichotomous UK Biobank morning person GWAS and the 23andMe morning person GWAS. The primary chronotype sample-size meta-analysis produced results for 15,880,941 variants in up to 697,828 individuals, with the secondary effect-size morning person meta-analysis producing results for 15,880,664 variants in up to 651,295 individuals . All reported meta-analysis P values were calculated by METAL using a Z-test.Meta-analysis was performed using the software package METAL37, DEPICT38, PASCAL36 and MAGMA34 to perform pathway and tissue enrichment. For MAGENTA and DEPICT, we included all variants from the meta-analysis, whereas for PASCAL, we included only those with an RSID as the software assigns variants to genes using their RSID. For the MAGENTA analysis, we used upstream and downstream limits of 110Kb and 40Kb to assign variants to genes by position, we excluded the HLA region from the analysis and set the number of permutations for gene-set enrichment analysis to 10,000. For DEPICT, we used the default settings and the annotation and mapping files provided with the software. As each of the four pieces of software adopts a different gene prioritisation method or relies on different databases, we included results from all four to cover all bases and to allow for better comparison with other studies, where only a single method may have been used. Briefly PASCAL corrects for the effect of LD blocks by accounting for the LD structure between associated variants, MAGENTA uses distance-based mapping but allows the user to set the upstream and downstream distances for inclusion, DEPICT makes use of large-scale data on gene co-regulation to prioritise genes before calculating enrichment in its own reconstituted gene sets and MAGMA, the most recent method (and implemented in the FUMA GWAS35 platform), claims greater statistical power to detect enriched gene sets than methods such as MAGENTA and PASCAL, without affecting the type 1 error rate. By using multiple methods and looking for consistency, we provide more compelling evidence of enrichment in specific pathways and tissues.We used MAGENTAhttps://github.com/bulik/ldsc/, to quantify the genetic overlap between the trait of interest and 222 traits with publicly available GWA data. Briefly, to estimate heritability of a single phenotype, LDSC regresses chi-squared statistics from summary statistics against pre-computed LD Scores (a measure of how well each variant tags nearby variants) for all variants of the phenotype. The genetic correlation (rg) between two phenotypes is, similarly, calculated by regressing each variant’s product of Z-scores from the two phenotypes against the LD scores; the slope of the regression line is the estimate of rg. The P values reported in this manuscript were calculated using a Z-test of calculated rg against the null hypothesis of rg = 0. Further methodological details are given elsewhere74. We used an LD-Score panel calculated in European samples from 1000 Genomes phase 3 v5 and removed variants that were not present in this reference panel. We considered any correlation as statistically significant if it had a Bonferroni-corrected P < 0.05.We used the LD-score regression (LDSC) software, available at 41 using a shotgun stochastic approach, allowing up to 20 causal SNPs at each locus and by focussing on a 1 Mb (±500 Kb) region around each index variant. As FINEMAP assumes a fixed sample size for all variants, we excluded variants not present in both the UK Biobank and 23andMe data, and to make the LD calculations more tractable we excluded variants with GWA analysis P > 0.01 to limit the total number of variants at each locus. We constructed an LD matrix for each locus by calculating the Pearson correlation coefficient for all pairs of variants using dosages derived from the unrelated European-ancestry subset of the UK Biobank imputed genotype probabilities . A variant was considered to be causal if its log10 Bayes factor was 2 or larger, a limit recommended by the FINEMAP documentation (http://www.christianbenner.com/index_v1.1.html).Fine-mapping analyses were performed using FINEMAP v1.1https://www.gtexportal.org/home/datasets) on 13/07/18, for significant associations. A variant was reported as an eQTL for a gene if the variant-gene association was significant  for one or more brain or non-brain tissues.We annotated variants identified by FINEMAP as likely to be causal using Alamut Batch v1.8  with genome assembly GRCh37 and all options set to default. We retained only the canonical (longest) transcript for each variant and reported the variant location and coding effect (if applicable) in this transcript. To identify whether variants were cis-eQTLs for nearby genes, we performed a lookup of our variants in the GTEx single-tissue cis-eQTL dataset (v7), accessed at the GTEx portal , with catalogues from three gene expression studies. Firstly, we used data from an RNAi screen of circadian clock modifiersChronotype exposure using the 351 variants and effect sizes discovered in this meta-analysis against the five significant psychiatric outcomes from the genetic correlation analyses and three metabolic outcomes, using summary data from published GWAS 75MR-Egger76Weighted median (WM)76Penalised weighted median (PWM)In both analyses, we tested four MR methods:56. We implemented the four MR methods listed above and also included the MR-Egger bootstrap to provide better estimates of the effect sizes and standard errors as compared to the MR-Egger method. We used data from published GWAS to test the effect of chronotype on the following exposures: schizophrenia77, major depressive disorder78, depressive symptoms79, subjective well-being79, PGC cross-disorder traits80, fasting insulin81, BMI82 and T2D84. To provide meaningful effect sizes for MR analyses, we used betas from the secondary effect size meta-analysis of the dichotomous UK Biobank and 23andMe morning person GWAS.Analysis 1 (chronotype exposure) was performed using the R package TwoSampleMR using aggregated summary statistics available through the MR-Base platform77, major depressive disorder85, insulin secretion86, favourable adiposity87, BMI55 and T2D88. As with analysis 1, chronotype effect sizes represented morningness liability and were taken from the secondary morning person meta-analysis, with the exception of the major depressive disorder exposure from a 23andMe study85 for which outcome effect sizes were taken from the UK Biobank-only chronotype GWAS.For analysis 2 (chronotype outcome) we applied the four MR methods listed above, utilising a custom pipeline. Using data from published GWAS, we tested whether chronotype is influenced by the following exposures: schizophreniaI.The strength of association of the genetic instruments with the risk factor is not correlated with the magnitude of the pleiotropic effects.II.The pleiotropic effects have an average value of zero.We used the inverse-variance weighted approach as our main analysis method and MR-Egger, weighted median estimation and penalised weighted median estimation as sensitivity analyses in the event of unidentified pleiotropy of our genetic instruments. MR results may be biased by horizontal pleiotropy, i.e., where the genetic variants that are robustly related to the exposure of interest (here chronotype) independently influence the outcome, through association with another risk factor for the outcome. IVW assumes that there is either no horizontal pleiotropy (under a fixed effect model) or, if implemented under a random effects model after detecting heterogeneity amongst the causal estimates, that:89 holds, in that it needs the pleiotropy of the genetic instruments to be uncorrelated with the instruments’ effect on the exposure. The weighted median approach is valid if less than 50% of the weight in the analysis stems from variants that are pleiotropic . Given these different assumptions, if all methods are broadly consistent this strengthens our causal inference. IVW causal effect size estimate P values were calculated using Student’s t test with (NSNP-1) degrees of freedom, MR Egger using Student’s t test with (NSNP-2) degrees of freedom and WM/PWM using a Z-test. Additional care should be taken interpreting results from binary exposures or outcomes, as these MR methods assume that horizontal pleiotropy due to within-category variation of dichotomous or categorical traits is negligible.MR-Egger provides unbiased causal estimates if just the first condition above holds, by estimating and adjusting for non-zero mean pleiotropy. However, MR-Egger requires that the InSIDE (Instrument Strength Independent of Direct Effect) assumptionSupplementary InformationPeer Review FileDescription of Additional Supplementary FilesSupplementary Data 1Supplementary Data 2Supplementary Data 3Supplementary Data 4Supplementary Data 5Supplementary Data 6Supplementary Data 7Supplementary Data 8Supplementary Data 9Supplementary Data 10Supplementary Data 11Supplementary Data 12Supplementary Data 13Supplementary Data 14Supplementary Data 15


M. m. musculus Y chromosomes into M. m. domesticus territory. To understand mechanisms facilitating Y spread, we created 31 recombinant lines from eight wild‐derived strains representing four localities within the two mouse subspecies. These lines were reciprocally crossed and resulting F1 hybrid males scored for five phenotypic traits associated with male fitness. Molecular analyses of 51 Y‐linked SNPs attributed ~50% of genetic variation to differences between the subspecies and 8% to differentiation within both taxa. A striking proportion, 21%  and 42% (frequencies of sperm tail dissociations), of phenotypic variation was explained by geographic Y chromosome variants. Our crossing design allowed this explanatory power to be examined across a hierarchical scale from subspecific to local intrastrain effects. We found that divergence and variation were expressed diversely in different phenotypic traits and varied across the whole hierarchical scale. This finding adds another dimension of complexity to studies of Y introgression not only across the house mouse hybrid zone but potentially also in other contact zones.Hybrid zones between divergent populations sieve genomes into blocks that introgress across the zone, and blocks that do not, depending on selection between interacting genes. Consistent with Haldane's rule, the Y chromosome has been considered counterselected and hence not to introgress across the European house mouse hybrid zone. However, recent studies detected massive invasion of  Following initial contact, genes that have diverged in allopatry are brought into novel combinations and tested for their effects on fitness. Natural selection will sieve the interacting genomes, incompatible combinations will be selected against and confined to the hybrid zone, neutral genes will diffuse freely to both sites, and selectively advantageous variants will recombine away from their native genomes and spread across the border into non‐native genetic background  where virgianus alleles of the Y‐linked Zfy gene spread into hemionus genome  as well as across the hybrid zone. In general, if Y chromosome variation is geographically structured and associated with variation in phenotypic traits, we might expect three alternative outcomes with respect to the Y introgression ability in distant replicates of the house mouse hybrid zone. First, there will be systematic asymmetric intersubspecific Y‐linked effects causing directional differences in fitness and this result will suggest uniformity of the Y introgression in the direction of the advantageous Y variant. Second, detection of intrasubspecific polymorphism in Y effects at various geographic regions will be indicative for different behavior of the Y within or across various replicates of the zone. Third, low phenotypic variance explained by geographically structured Y chromosome variation for a particular phenotypic trait will indicate the absence of association between the Y and a phenotype. In this case, the behavior of the Y in the hybrid zone and/or within the subspecies will be subject to neutral or random processes.To test the three alternatives conditioning the Y spread, we conducted a study in which sampling was designed to evaluate effects of the Y chromosome both at intra‐ and intersubspecific levels. Data were obtained from reciprocal F1 hybrids derived experimentally in the laboratory. Polymorphism was introduced by crossing eight wild‐derived mouse strains and mixing their genomes in a hierarchic way that allowed us to infer Y effects from the within‐strain to intersubspecific level. Fitness has many components and each of them can be affected by introduced polymorphism in different ways. As we documented that sperm‐related traits can affect the dynamics of the Y spread . Four strains represented The sampling of localities, from which in total more than 25 strains were developed, was designed a priori to mirror the increase of genetic variation with growing distance from the zone. The selection of eight strains was conditioned by statistical models used to test Y effects on phenotypes at various geographically structured levels (detailed below). The sampled localities are located symmetrically about 50 and 250 km from the estimated hybrid zone center Figure a.The parental strains were crossed in a combinatory design as depicted in Figure 2.2We succeeded in generating experimental males from 31 RLs. In total, 240 males were examined. Males were sacrificed by cervical dislocation and dissected at 60 days of age. One external measurement, body weight , was taken. The spleen was removed, weighed, and preserved in 96% ethanol for molecular analysis. The testes were weighed individually using analytical balances , and the values were averaged. Spermatozoa were released from the whole left epididymis, and the number of sperm heads was counted in ten squares of a Bürker chamber using an Olympus CX41 microscope under 200× magnification  containing 623,124 SNPs designed to capture genetic variation present in the laboratory mice , resulting variance estimates of corresponding random effects may be imprecise . Then, we split the data with respect to their Yssp origin and estimated differentiation between localities within each subspecies (Yloc level). Subsequently, we subdivided the data according to the Yloc level and compared strains within each locality (YWDS level). Finally, we assessed variation among the recombinant lines sharing Y chromosomes of the same strain origin  and had homogeneous variances . To compare groups of these variables, we used parametric tests: Welch's two samples t test and, at the YRL level, one‐way ANOVA supplemented with Tukey's post hoc test. Two frequency variables, DSH and ASH, were not distributed normally, and hence, they were analyzed by the non‐parametric Wilcoxon and Kruskal–Wallis tests, supplemented with the Nemenyi post hoc test at the YRL level. Type I error was set to 0.05; however, as we performed 15 subsidiary comparisons among means across all hierarchical levels, the significances were Bonferroni corrected . For the sake of transparency, we report both the uncorrected and corrected significances throughout the forthcoming text.In the second approach, experimental males’ data were partitioned in a downward sequence and compared stepwise based on the origin of their Y chromosomes as specified in Figure 33.1Genotypes at 51 SNPs are shown in Data 3.2R squared‐like values rendered by the hierarchical model (see Methods) is summarized in Table RL level, except for the DSH frequency, where higher variance is explained at the Yssp level. In SC and TW, the amount of the explained variance at the Yloc level nearly reaches the YRL level whereas it is zero or negligible at the YWDS and Yssp level, respectively. For two remaining variables, BW and ASH, the proportion of explained variance increases with increasing refinement of the tested model, that is, from the Yssp to YRL level, with exception of the Yloc, where no variance is explained. Details of GLMM estimates (parameter estimates for fixed effects and variances for random effects), their 95% bootstrap confidence, and R squared‐like statistics for each model term are listed in Data Phenotype data are available in Data 3.3All descriptive statistics  across all hierarchical levels are shown in Table domesticus males had a significantly higher frequency of DSH than the Ymusculus males. A similar difference was revealed in ASH although its significance (p = 0.014) disappeared after the Bonferroni correction  this high correlation being present at all levels of the analysis hierarchy. Interestingly, the higher frequency of abnormal sperm heads in domesticus males than in musculus males appeared to be driven by the YStraas males, whereas the ASH median for the YSchweben males did not differ from both musculus localities  being by more than two grams heavier than the YBULS males (L), representing roughly 10% of their body weight. A similar trend was observed between the YSTUS (S) and YSTUF (F) males, although the difference (p = 0.02) was not significant when Bonferroni corrected ; nevertheless, these differences were not significant after the Bonferroni correction , none of them remained significant after the Bonferroni correction.Splitting data according their Ys Figure a, with td Figure a. The YBa Figure b. The YBn Figure . No intrn Figure c. These s Figure d. Althou3.6STRA males where the difference between two RLs  appeared higher than 3 g, representing more than 20% of their BW , variation in TW only partly mirrored that observed in SC, and only one of the YSTUF males remained significant when Bonferroni adjusted . However, also this variation loses significance after the Bonferroni correction.Frequency of ASH displayed the lowest variation within the eight Y4Studies on spread of genetic variants and inference on selection in hybrid zones are focused on interactions between two divergent (sub)species. However, as we showed in this paper reducing analyses on (sub)species‐specific comparisons and neglecting intra(sub)specific variation can lead to oversimplification of the reality. We have created a set of recombinant lines that sample natural genetic polymorphisms within two house mouse subspecies, and by their reciprocal crossings, we produced F1 hybrid males. In this way, we partitioned variation in a set of phenotypic traits directly related to fitness into subspecific, local, between‐strain, and within‐strain Y‐associated effects. Of the three expected alternatives mentioned in Introduction , we found no support for the first one. On the contrary, we found compelling evidence for phenotypic polymorphism associated with Y chromosome variants. This variation was expressed diversely in different phenotypic traits and varied across the whole hierarchical scale. Before discussing the variable traits, however, we wish to make a note pointing to limits on data inference.The way we mixed the genomes and generated the F1 hybrids can only model a very short period after establishment of the house mouse contact zone. Consequently, studies of differential phenotypic performance in these hybrids cannot be conclusive in inferring introgressive advantage of the associated Y variants on non‐native genetic backgrounds. On the other hand, the results can be considered as indicative for the potential of some Y‐linked phenotypes to perform better than others after the secondary contact. This differential would then be a prerequisite for their subsequent spread.Another cautionary note relates to the strength of Y‐associated effects. We are aware that in all the traits under study, most of the variance remained unexplained Table . The res4.1domesticus compared to Ymusculus. DSH was the only trait in which the mixed model explained more variance at the subspecific level (Yssp) than at all other levels. The DSH medians were almost homogeneous on the lower scales. The increased variation in the recombinant lines bearing YSTRB implies an interaction between the Y‐linked gene(s) and other autosomal/X‐linked loci. As far as we know, susceptibility toward dissociation of sperm heads from tails has been examined only marginally. Nevertheless, our results are in agreement with the strength and directionality of the effect obtained in the study of White, Stubbings, Dumont, and Payseur (domesticus) and PWD (musculus) strain, the frequency of headless/tailless sperm was 0.38 in (PWD × WSB)F1, this value being significantly higher than 0.089 observed in the reciprocal F1 cross , displayed increased values in Y Payseur : In crosdomesticus males compared to the Ymusculus males was only significant without the Bonferroni correction. Most explained variance was detected among the RLs ; then, it was almost equally partitioned to the subspecific and strain levels . As almost 80% of variance remains unexplained, the Y‐associated effects cannot be explanatory variables themselves and they rather seem to interact with other quantitative trait loci. Hierarchical top‐down splitting of the variation revealed that the intersubspecific differentiation is driven through markedly increased variance of ASH in the YStraas males  and CBA  strains  and its congenic mutant strain B10.BR‐Ydel, with a partial deletion in the Y chromosome , LEWES, and WSB (both of the domesticus origin) F1 and (CZECHII × PWK)F1 males, the QTLs contributing to low sperm counts and abnormal sperm morphology were detected on various autosomes. Unfortunately, no data on X‐, Y‐, and mtDNA‐linked QTLs were presented .Although no subspecific effects were detected in sperm count (SC) and body weight (BW), these traits displayed substantial variation at the intrasubspecific  and intrastrain levels. Here, we will point to three phenomena connected with this variation. First, as anticipated, the absence of intersubspecific differentiation can result from pooling data of opposing effects from distinct localities. For example, averages of BW were found to be almost identical between the YBUSNA males represented the heaviest group of hybrids. As BW is a determinant of male competitive advantage, BW may facilitate the spread of the YBUSNA chromosomes. The direct effect of the Y chromosome on male body weight seems to be corroborated by the high proportion of explained variation . Nevertheless, high differentiation within the four recombinant lines sharing the same Y , significances of mtDNA effects on DSH would be the same as for the Y; however, the direction of the effect would be opposite; that is, the frequencies of DSH would be higher in the mtDNAmusculus males (having Ydomesticus) than in the mtDNAdomesticus/Ymusculus males. This would predict an advantage for the mtDNAdomesticus variant yet it is unclear how this advantage would pass from fathers to sons as mtDNA is transmitted maternally. Mitochondrial DNA is known to introgress across the house mouse hybrid zone in either direction . For example, most studies assessing the behavior of the Y in the mouse contact zone used loci within the non‐recombining region such as the Zfy2 gene (Macholán et al., Genetic polymorphism in Y chromosomes can be a clue for understanding the heterogeneity of opinions regarding introgressive behavior of the Y chromosome in the hybrid zone noted in Introduction. However, empirical and theoretical studies of the Y chromosome dynamics have usually been focused on binomial markers fixed for alternative variants in respective subspecies (here marked as the YUltimate knowledge on Y genetic variation can be obtained from long‐range sequencing. The Y chromosome is notoriously known for problems with sequencing due to low complexity regions and high copy number variation especially in the long Yq arm (Soh et al., 4.3domesticus and 4 musculus genomes separately within each subspecies. This design allowed, on average, two recombination events per chromosome within each subspecies. After generating intersubspecific F1 hybrids, we found that incorporating eight strains with four SNP‐defined Y haplotypes into the experimental crossing had a dramatic influence on phenotypic variation between and within mouse subspecies. Despite this effect, the introduced genetic variation and number of recombination events are only a tiny fraction of that which is expected to exist in hybrid zones. This finding adds another dimension of complexity to studies of Y introgression not only across the house mouse hybrid zone but potentially also in other secondary contact zones.In this study, we admixed 4 domesticus background.Analyses of various replicates of this zone have frequently built on a reduced one‐dimensional model based on distances from the zone center and introgression being measured as a cline shift of a locus in either direction (review in Baird & Macholán, IM conducted experimental crossing, animal maintenance, data collection, analysis, and visualization. LD participated in data collection. JK participated in data analysis. MM contributed to the result interpretation. JP designed the study. IM and JP wrote the manuscript with contribution of all other authors.All data and the R script used in this manuscript are available as electronic supplementary material. Click here for additional data file. Click here for additional data file. Click here for additional data file. Click here for additional data file. Click here for additional data file.


Several recent papers have reported strong signals of selection on European polygenic height scores. These analyses used height effect estimates from the GIANT consortium and replication studies. Here, we describe a new analysis based on the the UK Biobank (UKB), a large, independent dataset. We find that the signals of selection using UKB effect estimates are strongly attenuated or absent. We also provide evidence that previous analyses were confounded by population stratification. Therefore, the conclusion of strong polygenic adaptation now lacks support. Moreover, these discrepancies highlight (1) that methods for correcting for population stratification in GWAS may not always be sufficient for polygenic trait analyses, and (2) that claims of differences in polygenic scores between populations should be treated with caution until these issues are better understood.Editorial note: This article has been through an editorial process in which the authors decide how to respond to the issues raised during peer review. The Reviewing Editor's assessment is that all the issues have been addressed (ddressed . In recent years, there has been great progress in understanding the polygenic basis of a wide variety of complex traits. One significant development has been the advent of ‘polygenic scores’, which aim to predict the additive genetic component of individual phenotypes using a linear combination of allelic contributions to a given trait across many sites. An important application of polygenic scores has been the study of polygenic adaptation—the adaptive change of a phenotype through small allele frequency shifts at many sites that affect the phenotype.Thus far, the clearest example of polygenic adaptation in humans has come from analyses of polygenic scores for height in Europe. However, as we will show here, this signal is strongly attenuated or absent using new data from the UK Biobank , callingStarting in 2012, a series of papers identified multiple lines of evidence suggesting that average polygenic scores for height increase from south-to-north across Europe . AnalyseAll such studies rely on estimates of individual allelic effects on height, as calculated from genome-wide association studies (GWAS). These GWAS estimates are then combined with population-genetic analysis to test for selection. Under a null model of no directional change, we would not expect ‘tall’ alleles to increase (or decrease) in frequency in concert; thus, loosely speaking, a systematic shift in frequency of ‘tall’ alleles in the same direction has been interpreted as evidence for selection.While our focus here is on the the distribution of height polygenic scores in Europe, we see this as a case study for understanding the challenges in comparing polygenic scores across populations in general. Compared to other complex traits, height is particularly well-characterized, and the evidence for adaptation of height in Europeans seemed clear. Thus our work highlights a need for caution in this area until these issues are more fully understood .Until recently, the largest height GWAS dataset came from the GIANT consortium  with genotype and phenotype data for nearly 500,000 residents of the United Kingdom . UKB hasThis paper has two aims. First, we will show that previously reported signals of directional selection on height in European populations generally do not replicate when using GWAS effect estimates from the UK Biobank. Similar findings have been obtained independently by other groups working in parallel . Second,The conclusion that adaptation signals in GIANT were spurious has broader implications for GWAS analysis, as it indicates that standard approaches for population structure correction may not always be sufficient, and that further study is needed to understand their limitations. While we anticipate that current methods are likely adequate for many applications, in particular for identification and broad-scale localization of strong genotype-phenotype associations—they may be insufficient for applications such as phenotypic prediction and the detection of polygenic adaptation as these can be highly prone to the cumulative bias through uncorrected structure. Such analysis should be undertaken with great care.We downloaded or generated seven different height GWAS datasets, each relying on different subsets of individuals or using different analysis methods. The bold-faced text give the identifiers by which we will refer to each dataset throughout this paper. These include two previous datasets that show strong evidence for polygenic adaptation, as well as an updated version of the R15-sibs dataset released in response to results in the initial preprint version of this manuscript:GIANT:  .UKB-Eur:  signal of selection for increased height in the British population, previously reported by Using both GIANT and R15-sibs, This tSDS trend is greatly attenuated in all four GWAS versions performed on the UK Biobank sample , as well dataset .We wondered whether the main reason for the weakened trend in UKB-GB is an overly conservative PC-correction. This could occur if the genetic contribution to height is highly correlated with population structure axes. If this were the case, we would expect the correlation between GWAS p-value and tSDS to still be observed in a UKB GWAS without population structure correction . However, we see no evidence for this correlation (block jackknife p = 0.6). Taken together with the UKB-GB-NoPCs polygenic score analysis , the lacLastly, we examined tSDS at the most significant height-associated SNPs of each UKB GWAS . Significant SNPs show a positive average tSDS  and Tuscan (TSI) samples as proxies for northern and southern ancestry respectively. To control for the correlation between allele frequencies and LD Score, we normalized the frequency differences to have variance 1 within 1% average minor allele frequency bins. For shorthand, we refer to this measure as [GBR-TSI]. Under a model of selection driving allele frequency differences, we would expect the covariance of [GBR-TSI] and effect sizes to increase with LD Score. To test this, we regressed the product [GBR-TSI] In contrast to SDS, we find that none of the GWAS datasets show a strongly positive slope : the slodatasets , and fordatasets . We see The original LD Score regression paper noted that in the presence of linked selection, allele frequency differentiation might plausibly increase with LD Score. However, they concluded that this effect was negligible in the examples they considered , and sub2 is significantly correlated with LD Score (2 (2 and the squared Irish vs. White British contrast) are much more tightly correlated with LD Score than that of more diverged populations [GBR-TSI]2, suggesting that the LD Score regression slope may be equally vulnerable to stratification involving closely related populations than for those that are more distantly related. Finally, the product [GBR-TSI] We find that the squared allele frequency difference [GBR-TSI]LD Score , demonstAs noted above, the correlation we observe between allele frequency differentiation and LD Score could be generated by the genome-wide effects of linked selection. While a range of different modes of linked selection likely act in humans, one of the simplest is background selection . BackgroIn Appendix 3, we derive a simple model for the effect of BGS on the relationship between allele frequency divergence and LD Scores. Empirically, we find that LD Scores are positively correlated with the strength of background selection  McVicke, and thaWhat conclusions should we draw from our LD Score regression analyses? The significant positive intercepts observed for LD Score regression of both GIANT and R15-sibs with [GBR-TSI] suggest that both datasets suffer from confounding due to stratification along a north-to-south axis within Europe. These observations are consistent with the evidence presented in To summarize the key observations, we have reported the following:Multiple analyses based on GIANT and R15-sibs indicate strong signals of selection on height.However, the same signals of selection are absent or greatly attenuated in UK Biobank data. In some, but not all, analyses of frequency differentiation and SDS we still detect weakly significant signals of polygenic adaptation  and 2.The GIANT height GWAS is overall highly correlated with UKB-GB, but differs specifically by having an additional correlation with the main gradient of allele frequency variation across Europe, as modeled by frequency differences between GBR and TSI . LD ScorSelection signals in the R15-sibs data are consistent with, and in some cases even stronger, than the corresponding signals in GIANT, but are inconsistent with analyses using UK Biobank data. While correctly implemented sib-based studies are designed to be impervious to population structure, [GBR-TSI] LD Score analyses show a much stronger relationship between SDS and GIANT or R15-sibs than between SDS and UKB-GB. LD Score regression is generally considered to be robust to population structure  that effect sizes they released from their 2015 study were strongly affected by population stratification due to a bug. Furthermore, they have now stated that the effect sizes that they released publicly in 2016 were not the effect sizes used in their 2015 paper. As part of our own investigation, we have independently confirmed that sib-studies conducted using PLINK v1.90b5 are robust to environmental stratification . Our anaGIANT was conducted as a collaboration among a large number of research groups that provided summary statistics to the overall consortium. While the overall value of this pioneering dataset is not in question, it would not be surprising in retrospect if this GWAS were impacted by residual stratification along major axes of population structure.Lastly, we must conclude that the strong signal of LD Score genetic covariance between SDS and both GIANT and R15-sibs is largely spurious. This would imply that the LD Score regression slope is not robust to population structure confounding. Specifically, we demonstrated that background selection—through its correlation with LD Score—can potentially generate a spurious LD Score regression slope.Taken together, these observations lead us to conclude that what once appeared an ironclad example of population genetic evidence for polygenic adaptation now lacks any strong support. That said, there is still strong evidence that typical GWAS, including GIANT, do capture genuine signals of genotype-phenotype associations. For example, GWAS datasets regularly show strong functional enrichments of heritability within active chromatin from trait-relevant tissues , and theNonetheless, we have shown that GIANT effect-size estimates contain a component arising from stratification along a major axis of European population structure , and oneThese issues are apparent even within our UK Biobank results, where we see marked differences between results based on UKB-GB and UKB-Eur . The stuThe study of polygenic scores across ancestry and environmental gradients offers a range of promises and pitfalls . Lookingplink v. 2.0  and missing genotype rate of 0.05 (--geno 0.05), but otherwise with default parameters. Additionally, a firth adjusted logistic regression   were assng plink  with a Hgression  was run --hwe 1e-6) and missing genotype rate of 0.05 (--geno 0.05).Unrelated individuals, defined using estimates from KING , who sel1000 Genomes website, and VCF files for the Human Origins dataset were downloaded from the ‘Affymetrix Human Origins fully public dataset’ link on the Reich lab website and subsequently imputed to full genomes using the Michigan imputation server , conducted by https://data.broadinstitute.org/alkesgroup/UKBB/The UK Biobank GWAS of individuals of broadly European ancestral (UKB-Eur), conducted by http://cnsgenomics.com/data.htmlSibling GWAS data from https://github.com/jjberg2/height-data.Copies of these datasets are independently archived at:  In the interests of transparency, eLife includes the editorial decision letter, peer reviews, and accompanying author responses.Editorial note: This article has been through an editorial process in which the authors decide how to respond to the issues raised during peer review. The Reviewing Editor's assessment is that all the issues have been addressed.][eLife. Your article has been reviewed by three peer reviewers, including Magnus Nordborg as the Reviewing Editor and Reviewer #1, and the evaluation has been overseen by Mark McCarthy as the Senior Editor. The following individuals involved in review of your submission have also agreed to reveal their identity: Nicholas H Barton (Reviewer #2) and Joachim Hermisson (Reviewer #3).Thank you for submitting your article "Reduced signal for polygenic adaptation of height in UK Biobank" for consideration by The Reviewing Editor has summarized the major concerns shared by all reviewers, and we have also included the separate reviews below for your consideration.If you have any questions, please do not hesitate to contact us.Summary:This is one of two papers demonstrating that published signals of selection on human height cannot be replicated in the recently released UK Biobank data, apparently because these signals were caused by confounding population structure that is absent in UK Biobank data.Major concerns:We were struck by how both papers focus on spurious signals of selection rather than the underlying cause, which is that the GWAS effect-size estimates are confounded. The former is a somewhat esoteric question, but the latter may have enormous implications for much of human genetics, and these papers are likely to be heavily cited because of this. However, the papers seem to go out of their way to avoid discussing this topic. Of course we are not the authors, but, for the record, it looks odd.Furthermore, the papers seem to suggest that confounding is not present in the UK Biobank data, but isn't it more likely that the magnitude is simply smaller?The papers also present evidence that a sib-based study by Robinson et al., 2015, that was meant to eliminate confounding did no such thing. This is disturbing, and while we understand that identifying the reason may be beyond the present papers, the general implications should again probably be discussed.Finally, while this is a carefully written and extremely scholarly paper, it relies heavily on population genetics jargon, and will be difficult to read for outsiders. We suggest substantial editing with this in mind.Separate reviews (please respond to each point):Reviewer #1:This one of at least two papers appearing simultaneously and reaching exactly the same conclusion. It is well written, although perhaps a bit too technical for people not directly working in the field of human population genetics.The only thing that surprises me about this paper is that it, as well as the other one I have seen, focuses on the relatively obscure issue of whether height has been under selection, tiptoeing around the much bigger issue (the elephant in the room) that the reason the claims for selection do not stand is that the GWAS estimates of effect sizes are biased because of population structure. It is not just the selection signals that do not replicate, but the polygenic scores. I'm not surprised, but, as you know, there are probably at least a hundred papers out there that are based on the infallibility of LD Score regression and genomic prediction. I understand the need for caution before attacking this edifice, but I nonetheless think some clarification is unavoidable.Reviewer #2:This is a carefully argued and scholarly examination of why estimates of selection, based on "polygenic scores", are weaker in the UK Biobank data than in earlier studies. This is an important issue, and so even though the causes of the discrepancy are not at all clear, the paper will be an important contribution. I have various comments below, and on the annotated PDF; several of these ask for a clearer definition of terminology that will make the paper more accessible to those not immersed in the field.I would be encouraged by seeing a simulation of a stratified population, in which the standard correction for stratification fails, as is claimed to be the case here. One would also like to have some idea of what strength of allele frequency differentiation is needed to generate the observed differences in polygenic scores, and whether (as claimed) this indeed does not much affect GWAS estimates. However, this might be a non-trivial exercise, so I would not insist on it. I would like to see some discussion of how such a study could be approached, though.The lesson from this is that it is extremely hard to reliably detect selection through the accumulation of slight changes in allele frequency. However, one should bear in mind that selection on polygenic traits is effective through precisely this process, and is largely unaffected by population structure. This is remarkable, but not paradoxical: natural selection can be effective even when its genetic basis cannot be identified.Minor Comments:Abstract: "polygenic differences netween populations" is perhaps ambiguous. You are not referring to differences in breeding value here, but to differences in BV inferred from SNP frequencies. Perhaps that can be said more directly.Introduction first paragraph: Actually, polygenic scores predict an individual's additive genetic component, which is not the same as "individual phenotypes". Perhaps this could be explained: other studies of QG in the wild emphasise the importance of this distinction.Subsection “GWAS data used to study adaptation of height” paragraph five: SDS only gets defined in the Table, it needs explanation in the text.Subsection “Weak replication in UK Biobank” How confident can we that "current methods are likely sufficient for most applications" ? As noted above, I would have more confidence in this if we understood better how population structure confounds signals of polygenic adaptation.Results section (and elsewhere): "genetic correlations" needs to be defined explicitly, correlations of what with what? Do these strong correlations imply that there is no detectable difference in effect size between populations? What bounds can one put on effect size differencesFigure 1: Best to label axes "Latitude, European" and "Longitude, Eurasian"Subsection “SDS signal of selection in Britain.”: Define LMM! Since the correction for structure is crucial, it needs to be explained clearly early on.Subsection “Relationship between GWAS estimates and European population structure”: Can one estimate the predicted strength of the "winner's curse"?Subsection “LD Score regression signal”: "Meanwhile, confounders such as population structure are expected to affect SNPs of different LD Score equally": It is not obvious to me that this is the case.Subsection “Summary of LD Score Regression Results”, final sentence: Delete "going forward"Discussion section paragraph five: Nevertheless, one would like to know how much stratification may influence the accuracy of GWAS estimates.a. Therefore, we can estimate its effect on pairwise LD, which will be very small because there are so may pairs, but may nevertheless lead to some overall bias. More directly, is there any correlation in polygenic scores between parents, consistent with the known assortment? One might be able to separate out causes of assortment in this way: stratification vs true assortment, causally due to height.Subsection “Expanded SNP Sets” final paragraph: One should be able to quantify this. We know the strength of assortment for height, and its effect on VReviewer #3:Both manuscripts by Berg et al. and Sohail et al. present thorough and insightful analyses with highly relevant results for current and future GWAS studies. Even prior to publication, the manuscripts have considerable impact. They will be widely read and cited. I do not think that further analyses are needed, with the potential exception of the third point below. All other points concern the discussion, in particular the guidance for further research that will surely emerge from these studies.# How safe are results based on the UK Biobank data?This refers to the weak signals reported (with much caution) in the present studies, but also to potential future results on other traits. You recommend using data "such as UKB" and we will certainly see many more studies based on this resource. I would therefore appreciate a more specific discussion of risks connected to this particular data set.1) Stratification even within the UKB-GB data: It is well known that height and socioeconomic status are correlated in modern societies , and social status correlates with descent. In the UK, both factors are also geographically stratified, with people living in the north of the country having lower socioeconomic status and shorter stature, on average, than those in the south. Furthermore, the percentage of Anglo-Saxon admixture varies across the UK. How could these factors influence results based on UKB data, both here and otherwise?2) Potential influence of GxE interactions: The manuscripts focus (for good reason) on issues connected with stratification. However, if polygenic scores depend on the environment , GxE interactions are an alternative confounding factor. Importantly, use of a homogeneous detection panel (to avoid stratification), such as UKB-GB, could increase these effects. Maybe this should be briefly discussed in the context of the present results and mentioned as a necessary caveat also for future studies that use detection panels from narrow geographic regions.# What, exactly, causes the problems with the previous data?3) There seem to be two relevant differences of the GIANT data relative to UKB: 1) UKB is much more homogeneous and 2) GIANT is a meta-study, collecting summary statistics from many sources that are individually corrected for stratification. One would like to know better which factor is decisive. This could be further addressed by combining summaries from sub-samples of the "UKB-all" data in an artificial meta-study.4) The Robinson et al., 2015 GWAS: Sib-based studies are done to avoid/minimize stratification effects and the Robinson 2015 data have been used as a proof of robustness in several previous studies. The fact that you find clear signs of stratification is sobering and one would like to know what has gone wrong. You may not currently have any explanation and this is fair enough. However, the discussion should be clearer and say upfront that results based on these data cannot be trusted until we understand the issues.Minor Comments:2 in Figure 3C is strange. Any idea?a) The very low rb) Figure 4: I was looking for the analysis using the other GB datasets, turns out that this is done in the supplementary information, but you should briefly comment on the results in the results part of the main text.Additional data files and statistical comments:Everything is well explained and all newly generated GWAS data are on Dryad. Major concerns:We were struck by how both papers focus on spurious signals of selection rather than the underlying cause, which is that the GWAS effect-size estimates are confounded. The former is a somewhat esoteric question, but the latter may have enormous implications for much of human genetics, and these papers are likely to be heavily cited because of this. However, the papers seem to go out of their way to avoid discussing this topic. Of course we are not the authors, but, for the record, it looks odd.One issue for us in writing this paper is that the effect at individual SNPs is relatively small, but systematic, therefore it is unclear how strongly various other types of analyses based on GWAS will be affected. This uncertainty means that in laying out the implications in a reasonable way we erred toward being conservative. We have now expanded our discussion to more broadly discuss the implications for polygenic score predictions, beyond just the spurious signals of selection, where the implications are clearer.Furthermore, the papers seem to suggest that confounding is not present in the UK Biobank data, but isn't it more likely that the magnitude is simply smaller?As discussed below we now point to evidence of residual confounding in the biobank.The papers also present evidence that a sib-based study by Robinson et al., 2015, that was meant to eliminate confounding did no such thing. This is disturbing, and while we understand that identifying the reason may be beyond the present papers, the general implications should again probably be discussed.Two weeks ago, Robinson and colleagues informed us that the effect sizes they released in 2016 had serious stratification issues due to a bug (see statement posted here: http://cnsgenomics.com/data.html). Furthermore, they revealed that these effect sizes that they released associated with their 2015 paper, were not in fact the effect sizes they used their 2015 paper. They also released a third set of effect sizes produced by reanalyzing the sibling data. This news obviously came to us late in our revisions process, but we have now run their new 2018 set of effect sizes through our pipeline. We now see no consistent signal of selection in Robinson et al’s new set of effect sizes, consistent with our BioBank analyses. Thus at least one mystery has now been solved.Finally, while this is a carefully written and extremely scholarly paper, it relies heavily on population genetics jargon, and will be difficult to read for outsiders. We suggest substantial editing with this in mind.We have substantially edited the paper to define terms, and make sure that it is more accessible.Separate reviews (please respond to each point):Reviewer #1:This one of at least two papers appearing simultaneously and reaching exactly the same conclusion. It is well written, although perhaps a bit too technical for people not directly working in the field of human population genetics.The only thing that surprises me about this paper is that it, as well as the other one I have seen, focuses on the relatively obscure issue of whether height has been under selection, tiptoeing around the much bigger issue (the elephant in the room) that the reason the claims for selection do not stand is that the GWAS estimates of effect sizes are biased because of population structure. It is not just the selection signals that do not replicate, but the polygenic scores. I'm not surprised, but, as you know, there are probably at least a hundred papers out there that are based on the infallibility of LD Score regression and genomic prediction. I understand the need for caution before attacking this edifice, but I nonetheless think some clarification is unavoidable.We have now extended our discussion of the issues for polygenic scores in the discussion, and how stratification is a strong source of false among-population variance for studies for samples with variation along axes of European variation.Reviewer #2:This is a carefully argued and scholarly examination of why estimates of selection, based on "polygenic scores", are weaker in the UK Biobank data than in earlier studies. This is an important issue, and so even though the causes of the discrepancy are not at all clear, the paper will be an important contribution. I have various comments below, and on the annotated PDF, several of these ask for a clearer definition of terminology that will make the paper more accessible to those not immersed in the field.We have incorporated the reviewer’s comments about clarifying terminology throughout the document.I would be encouraged by seeing a simulation of a stratified population, in which the standard correction for stratification fails, as is claimed to be the case here. One would also like to have some idea of what strength of allele frequency differentiation is needed to generate the observed differences in polygenic scores, and whether (as claimed) this indeed does not much affect GWAS estimates.. However, this might be a non-trivial exercise, so I would not insist on it. I would like to see some discussion of how such a study could be approached, though.We agree that it would be useful to offer some simulations to show how stratification affected the original GWAS. However, the issue is that the source of population stratification in the meta-analysis is far from clear, as it involves many studies, each of which performed some level of correction for stratification. As such we feel that any simulation would not really provide much intuition about the level of confounding involved in the original GWAS.The lesson from this is that it is extremely hard to reliably detect selection through the accumulation of slight changes in allele frequency. However, one should bear in mind that selection on polygenic traits is effective through precisely this process, and is largely unaffected by population structure. This is remarkable, but not paradoxical: natural selection can be effective even when its genetic basis cannot be identified.Minor Comments:Abstract: "polygenic differences netween populations" is perhaps ambiguous. You are not referring to differences in breeding value here, but to differences in BV inferred from SNP frequencies. Perhaps that can be said more directly.Changed to “differences in polygenic score between populations”Introduction first paragraph: Actually, polygenic scores predict an individual's additive genetic component, which is not the same as "individual phenotypes". Perhaps this could be explained: other studies of QG in the wild emphasise the importance of this distinction.Changed to “additive genetic component of individual phenotypes”Subsection “GWAS data used to study adaptation of height” paragraph five: SDS only gets defined in the Table, it needs explanation in the text.Fixed.Subsection “Weak replication in UK Biobank”: How confident can we that "current methods are likely sufficient for most applications" ? As noted above, I would have more confidence in this if we understood better how population structure confounds signals of polygenic adaptation.Changed “most” to “many”, and outlined a few contrasting cases where current methods seem likely sufficient, vs. those where they may not be.Results section (and elsewhere): "genetic correlations" needs to be defined explicitly, correlations of what with what? Do these strong correlations imply that there is no detectable difference in effect size between populations? What bounds can one put on effect size differencesAdded text explaining the procedure for calculating “genetic correlations”, and how we are interpreting them.Figure 1: Best to label axes "Latitude, European" and "Longitude, Eurasian"Done.Subsection “SDS signal of selection in Britain.”: Define LMM! Since the correction for structure is crucial, it needs to be explained clearly early on.Done.Subsection “Relationship between GWAS estimates and European population structure”: Can one estimate the predicted strength of the "winner's curse"?10.1002/gepi.20398), to correct for the winner’s curse, but it’s unclear to us in our current application what the practical advantage of doing so would be.It is possible, but not trivial , which argued that the rate of drift and LD Score should be uncorrelated. They acknowledged that background selection could potentially violate this argument, and performed a few simulations in small samples of northern Europeans to support it. This assertion of independence between rate of drift and LD Score has been generally accepted by the human genetics community. However, as we show later in this paper, this assumption does not necessarily hold.We replaced the word “expected” with “argued” to clarify that we do not ourselves necessarily expect this to hold, but that it has been argued.Subsection “Summary of LD Score Regression Results”, final sentence: Delete "going forward"Done.Discussion section paragraph five: Nevertheless, one would like to know how much stratification may influence the accuracy of GWAS estimates.We have updated this section of the paper to more thoroughly discuss our current state of knowledge.a. Therefore, we can estimate its effect on pairwise LD, which will be very small because there are so may pairs, but may nevertheless lead to some overall bias. More directly, is there any correlation in polygenic scores between parents, consistent with the known assortment? One might be able to separate out causes of assortment in this way: stratification vs true assortment, causally due to height.Subsection “Expanded SNP Sets” final paragraph: One should be able to quantify this. We know the strength of assortment for height, and its effect on VThis is an interesting idea that we think may be worth pursuing in the future. However, we note that the accelerated rate of drift relative to our neutral expectation depends on the degree of assortative mating in the past, when the specified drift was taking place, and may therefore differ from the rate that would be expected given the present day degree of assortative mating. The best that can likely be estimated from this sort of signature is some sort of time averaged rate of assortative mating over the period during which the populations under study were diverging.This does raise the point that, so long as stabilizing selection is not too strong, strong assortative mating over short periods of time may be essentially indistinguishable from bouts of selection. This is a topic some of us are interested in exploring in the future.Reviewer #3:Both manuscripts by Berg et al. and Sohail et al. present thorough and insightful analyses with highly relevant results for current and future GWAS studies. Even prior to publication, the manuscripts have considerable impact. They will be widely read and cited. I do not think that further analyses are needed, with the potential exception of the third point below. All other points concern the discussion, in particular the guidance for further research that will surely emerge from these studies.# How safe are results based on the UK Biobank data?This refers to the weak signals reported (with much caution) in the present studies, but also to potential future results on other traits. You recommend using data "such as UKB" and we will certainly see many more studies based on this resource. I would therefore appreciate a more specific discussion of risks connected to this particular data set.1) Stratification even within the UKB-GB data: It is well known that height and socioeconomic status are correlated in modern societies , and social status correlates with descent. In the UK, both factors are also geographically stratified, with people living in the north of the country having lower socioeconomic status and shorter stature, on average, than those in the south. Furthermore, the percentage of Anglo-Saxon admixture varies across the UK. How could these factors influence results based on UKB data, both here and otherwise?We now have a brief discussion of remaining stratification in the UK Biobank, and point to other papers on this topic.2) Potential influence of GxE interactions: The manuscripts focus (for good reason) on issues connected with stratification. However, if polygenic scores depend on the environment , GxE interactions are an alternative confounding factor. Importantly, use of a homogeneous detection panel (to avoid stratification), such as UKB-GB, could increase these effects. Maybe this should be briefly discussed in the context of the present results and mentioned as a necessary caveat also for future studies that use detection panels from narrow geographic regions.This is a fair point, but also one that has been covered fairly extensively in the Berg and Coop 2014 paper, as well as the recent 2018 commentary from Novembre and Barton. We now include a comment regarding the promises and pitfalls of studying polygenic phenotypes across ancestry and environmental gradients in our closing paragraph, and direct readers to these two papers.# What, exactly, causes the problems with the previous data?3) There seem to be two relevant differences of the GIANT data relative to UKB: 1) UKB is much more homogeneous and 2) GIANT is a meta-study, collecting summary statistics from many sources that are individually corrected for stratification. One would like to know better which factor is decisive. This could be further addressed by combining summaries from sub-samples of the "UKB-all" data in an artificial meta-study.We agree this would be interesting. However, a thorough investigation of this issue could easily constitute an entire paper of its own, and without access to the original GIANT cohort data, would bring us no closer to determining what actually happened in that dataset.4) The Robinson et al., 2015 GWAS: Sib-based studies are done to avoid/minimize stratification effects and the Robinson 2015 data have been used as a proof of robustness in several previous studies. The fact that you find clear signs of stratification is sobering and one would like to know what has gone wrong. You may not currently have any explanation and this is fair enough. However, the discussion should be clearer and say upfront that results based on these data cannot be trusted until we understand the issues.Robinson et al. have now informed us that the summary statistics they posted online in 2016 were A) not the same statistics actually used in their 2015 paper, and B) afflicted by a plink bug which resulted in mishandling of family structured data, and therefore no control for population structure (http://cnsgenomics.com/data.html). We have updated the paper throughout to reflect this, and we added an analysis of a new set of corrected summary statistics they released.Minor Comments:2 in Figure 3C is strange. Any idea?a) The very low rThis is due to the substantially lower power of the Robinson sib study relative to GIANT. This should result in a greater distance, on average, between the chosen lead SNP and the causal variation it tags, leading to much weaker replication of effect sizes. We have added a comment on the difference in power to the figure caption.b) Figure 4: I was looking for the analysis using the other GB datasets, turns out that this is done in the supplementary information, but you should briefly comment on the results in the results part of the main textAdded.