key: cord-0951305-h3qceu3j
authors: Aron, Janine; Muellbauer, John
title: Excess Mortality Versus COVID‐19 Death Rates: A Spatial Analysis of Socioeconomic Disparities and Political Allegiance Across U.S. States
date: 2022-02-21
journal: Rev Income Wealth
DOI: 10.1111/roiw.12570
sha: 9f2b18e50fb7906cf938f307f7de28c5b6371dc5
doc_id: 951305
cord_uid: h3qceu3j

Excess mortality is a more robust measure than the counts of COVID‐19 deaths typically used in epidemiological and spatial studies. Measurement issues around excess mortality, considering data quality and comparability both internationally and within the U.S., are surveyed. This paper is the first state‐level spatial analysis of cumulative excess mortality for the U.S. in the first full year of the pandemic. There is strong evidence that, given appropriate controls, states with higher Democrat vote shares experienced lower excess mortality (consistent with county‐level studies of COVID‐19 deaths). Important demographic and socio‐economic controls from a broad set tested were racial composition, age structure, population density, poverty, income, temperature, and timing of arrival of the pandemic. Interaction effects suggest the Democrat vote share effect of reducing mortality was even greater in states where the pandemic arrived early. Omitting political allegiance leads to a significant underestimation of the mortality disparities for minority populations.

Excess mortality is a count of deaths from "all causes" expressed relative to the benchmark of "normal" deaths. "Normal" death rates reflect persistent factors such as the age composition of the population, the incidence of smoking and air pollution, the prevalence of obesity, poverty and inequality, and the normal quality of health service delivery. Normal deaths are typically estimated from several years of data on pre-pandemic mortality using methods of varying sophistication.

In a pandemic, deaths rise sharply, but causes are often inaccurately recorded, particularly when reliable tests are not widely available. Thus, the death counts 1 attributed to COVID-19 may have been significantly understated. Excess mortality data overcome two problems in reporting COVID-19-related deaths. Miscounting from the misdiagnosis or under-reporting of COVID-19-related deaths is avoided. Excess mortality data also include "collateral damage" from other health conditions, left untreated if the health system is overwhelmed by COVID-19 cases, or from deliberate actions that prioritize patients with COVID-19 over those with other symptoms. Precautionary measures taken by governments and individuals may also influence death rates in a pandemic. Deaths from traffic accidents and deaths from other infectious diseases such as influenza may decline; however, suicide rates may rise. 2 Excess mortality captures the net outcome of all these factors.

Excess mortality data can be used to draw lessons from cross-country and within-country differences and to analyze the social and economic consequences of the pandemic and of lockdown restrictions. Excess death figures may help to avoid the measurement biases inherent in other data typically used to estimate the virus reproduction rate, R, in epidemiological models, 3 crucial for designing and assessing non-pharmaceutical interventions such as lock-downs.

Studies comparing the U.S. to other countries find that in 2020 it ranked amongst the highest in COVID-19 deaths per 100,000 (Bilinski, 2020) and in rates of excess deaths (OECD paper by Morgan et al. (2020) , ONS (2021a) and earlier versions, and Aron and Muellbauer (2020c) ). Woolf et al. (2020 Woolf et al. ( , 2021 , comparing U.S. mortality from COVID-19 (March-October, 2020) to leading causes of death two years before the pandemic (March-October, 2018) , find that COVID-19 was one of the leading causes of death; in the Spring and late Autumn of that year, it was the leading cause of death in the U.S. The pandemic is likely to exacerbate the decline in life expectancy that has been apparent since 2014 (Koh et al., 2020) .

Virtually all spatial analyses of mortality in the U.S. are based on counts of COVID-19 deaths. The only exception is a county-level study of excess mortality by Stokes et al. (2021) , of which more below. Davies et al. (2020) is an excellent spatial study of excess mortality in England. An indication of the limitations and biases in the data on infections and COVID-19 deaths is given in IHME (2021), who suggest that death counts are a less biased estimate of true COVID-related deaths than COVID-19 case counts are of the true number of infections. 4 Yet, Weinberger et al. (2020) find that official tallies likely undercount U.S. deaths due to the virus, with the completeness of the tallies varying markedly between states; they also advocate excess all-cause mortality data as more reliable to estimate the full COVID-19 burden. 1 For example, see webpage: COVID-19 Dashboard by the Center for Systems Science and Engineering (CSSE), Johns Hopkins University (JHU). https://www.arcgis.com/apps/opsda shboa rd/ index.html#/bda75 94740 fd402 99423 467b4 8e9ecf6

2 Other examples are increases in self-harm, domestic abuse and other crime; use of tobacco, drugs and alcohol; and anxiety and changed quality of diet from loss of jobs and income, see Kontis et al. (2020) . 3 See the evidence of Prof. John Edmunds to the UK Science and Technology Parliamentary Select Committee on 7 May 2020. He explained that while excess mortality data lag COVID-19 infections, the data are an important check on earlier estimates of the rate of spread of the virus. 4 Case count data are affected by differences in treatment-seeking behavior, testing protocols and access to care, and further compromised by infectious asymptomatic individuals or pre-symptomatic individuals. Testing results may be compromised by accuracy concerns.

In the first 52 weeks of the pandemic, there were around 650,300 excess deaths in the U.S., compared with COVID-19 deaths of around 499,500, sourced from Coronavirus Resource Center, Johns Hopkins University (JHU), or around 530,000, when sourced from the U.S. Centers for Disease Control and Prevention (CDC). Figure 1 shows the time profile of weekly per capita excess deaths at the national level, and the ratio of the CDC count of COVID-19 deaths to excess deaths. This shows severe under-counting of COVID-19 deaths at the start of the pandemic in the Spring and suggests considerable under-counting in the Summer and early Autumn of 2020. The figure also shows the ratio of JHU-sourced COVID-19 deaths to CDC-sourced COVID-19 deaths; the high ratio suggests an even greater under-counting by the JHU source than the CDC source at the start of the pandemic. Moreover, the divergence between the two measures persists throughout the pandemic and is greatest at the peaks of the waves. Our empirical work on COVID-19 deaths suggests strongly that the CDC-sourced COVID-19 death count is preferable to the JHU data, see Section 5.4. Figure 2 ranks the U.S. states by the cumulated excess deaths per capita for the 52 weeks, comparing with the P-score, measuring the ratio of excess deaths to normal deaths, see Table 1 , and the CDC measure of per capita COVID-19 deaths. Comparing the COVID-19 death count to excess deaths across states reveals considerable variations in the degree of under-counting. Per capita excess deaths X − X population e.g. Kontis et al. (2020) , Woolf et al. (2020) Reasonable comparability but sensitive to the age distribution, as well as to socioeconomic differences between countries or regions Used in this paper. Used in Chen et al. (2019) The P-score X − X X e.g. Our World in Data website; ONS (2021b) regularly updated article Good comparability, though still affected by socioeconomic differences between countries or regions Used in this paper P-score: (X minus the expected value of X for the population), divided by the expected value of X for the population Notes: ** The Z-score calculation assumes a Poisson distribution, adjusted for excess dispersion to approximate the underlying probability distribution of weekly deaths. The Poisson is a discrete probability distribution that expresses the probability of a given number of events occurring in a fixed interval of time if these events occur with a known constant mean rate and independently of the time since the last event. The calculation both of normal deaths and the standard deviation is described in Farrington et al. (1996) . Our study focuses on cumulative U.S. excess mortality across 51 states (including Washington, D.C.) in the first 52 weeks of the pandemic. This avoids potential mismeasurement problems in the usual dependent variables, and we compare the results with a model for COVID-19 deaths per capita. One reason for the choice of state comparisons is that the U.S. CDC (Centers for Disease Control and Prevention) does not generate county-level estimates of excess mortality. 5 We have found only two spatial analyses of U.S. COVID-19-related mortality at the state level, IHME (2021) and Doti (2021) , 6 both modeling COVID-19 deaths. Thus, our paper is the first state-level spatial analysis of excess mortality, and the first state state-level spatial analysis of mortality that explicitly includes political variables. 7 There are several advantages to a state-level perspective, apart from a simpler and more easily interpretable spatial model. Using states can be justified by their crucial political role defined by the Constitution, e.g. their equal representation in the Senate and their role in the Electoral College, which elects the President. It is possible to flexibly explore different hypotheses without the significantly greater challenge faced by county studies of properly capturing complex local spatial correlation. Few county studies deal seriously with county spill-over effects. The use of state fixed effects in county models can help address such flaws but they are difficult to interpret, and much of what is of central interest to policy can be thereby "washed out." While the state-focus has the obvious cost of the reduced range of spatial variation and fewer degrees of freedom, it provides a useful complement with implications for county-level research.

The heterogeneity across U.S. states in excess deaths linked to COVID-19 in the first 52 weeks was enormous, from 305 excess deaths per 100,000 persons in Mississippi, to 64 in Maine and 65 in Washington State, the two lowest on the mainland. Using the right controls for state-level comparisons is crucial to disentangle the effects of political partisanship from other determinants. Fortunately, there have been many studies at much more fine-grained spatial levels, e.g. over 3000 counties, from which the most important controls can be deduced. For the majority of studies (an exception is Stokes et al. (2021) ), the dependent variable is a per capita measure of the infection count and/or of COVID-19 deaths, see Table 1 . These dependent variables embody measurement bias, although some parameterisations in a dynamic model can reduce the bias subject to simplifying assumptions (e.g. Rubin et al. (2020)) . Five examples of cross-section spatial studies that include socio-demographic and health determinants, but do not include political variables, are Stokes et al. (2021) , Knittel and Ozaltun (2020) , McLaren (2020), Karmakar et al. (2021) at the county level, and Doti (2021) at the state level, who also includes state interventions on social © 2022 International Association for Research in Income and Wealth distancing. Considering also the role of partisanship and COVID-19 infections and deaths are Liao and De Maio (2021) and Desmet and Wacziarg (2021) . 8 A detailed critical review of these studies can be found in Aron and Muellbauer (2022) .

Structural differences between locations have had huge effects on mortality outcomes in the pandemic's first year. The potential determinants fall into four groups. A first set of pre-pandemic baseline population characteristics, used in many studies, affecting the transmission risk of contracting COVID-19, and vulnerability to the serious health consequences of infection and to non-pharmaceutical interventions by governments, are mostly likely to remain largely unchanged over the pandemic. 9 A second set of public health and social care determinants has been affected by rapid rescaling and reskilling to affect capacity. Over time there has been an improved understanding of the disease and its treatment; later, vaccines were deployed, and new virus variants encountered. A third set of factors comprises policies for lockdown and other restrictions, varying widely across states and countries, which have been tightened and relaxed at times over the different waves of the pandemic. A final set concerns citizens' compliance with policies which may also have altered over the pandemic, affected by the perception of economic tradeoffs, by changing scientific advice, and by the media and political role models. Generally, therefore, longitudinal spatial models, being dynamic, are expected to be subject to changing values over time of the coefficients of the last three sets of determinants, but also of the first set, to the extent that there may be correlations with omitted variables that themselves are subject to alteration. In a cross-section context, however, due to endogeneity issues, it is not possible to include contemporary restriction controls and other non-pharmaceutical interventions, or to include time-varying controls such as critical care capacity. However, it is possible to pick up some time-varying influences by testing for potential interaction effects, between controls like income, political allegiance and pre-pandemic critical care capacity with measures of the (exogenous) timing of first arrival of significant levels of infection.

Political partisanship, e.g. measured by the U.S. electoral vote share, has supplemented the controls in some county studies of pandemic deaths and case counts to proxy for private attitudes and compliance. Gollwitzer et al. (2020) summarize studies of partisanship, its measurement and the link with social judgments and behaviors (e.g. Van Bavel and Pereira (2018)). Allcott et al.

(2020) study partisan differences in Americans' surveyed beliefs concerning their infection risk and the likely severity of the pandemic, and find that social distancing behaviors reflect these beliefs. Makridis and Rothwell (2020) use nationally-representative U.S. panel data to demonstrate that the formation of 8 Of these studies, Karmakar et al. (2021) and Desmet and Wacziarg (2021) also have a dynamic aspect. Other studies introducing dynamics into the spatial analysis are Rubin et al. (2020 ), Gerritse (2020 , IHME (2021), Hamidi et al. (2020) , Gollwitzer et al. (2020) and Almagro et al. (2020 Almagro et al. ( , 2021 . 9 The baseline variables include demographic and health characteristics differentiated by gender; measures of poverty, income and inequality; racial and ethnic group status; employment status, type of occupation and working conditions; transport measures such as use of public transport, commuting across states and international linkages through airports; and housing density. Baseline variables concerning employment and transport, have, of course, evolved over the course of the pandemic.

© 2022 International Association for Research in Income and Wealth beliefs about the pandemic and social distancing behavior is driven primarily by political affiliation. Druckman et al. (2021) find a strong association between citizens' levels of partisan animosity and their attitudes about the pandemic, and the actions they take in response to it. Hamel et al. (2021) analyze the results of multiple surveys confirming the role of partisanship in explaining spatial differences in U.S. vaccination rates.

Omitted variables are likely to be the most prominent source of bias if they are correlated with the included regressors. The inclusion of political partisanship adds an important omitted variable to the more typical set of regressors, which are focused on the characteristics affecting transmission risk and vulnerability to infection and the preparedness and capacity of the public health and social care systems. As in other cross-section studies, there may be omitted variables that are correlated with an included regressor but are themselves difficult to measure. Examples are wealth inequality across race and racial discrimination, which may provide channels to explain the widely-found significance of racial and ethnic regressors in the above types of analyses, conditional on inclusion of a set of co-variates. 10 Another example is that the accidental early arrival of the pandemic in certain counties and states-because of returning travelers from Europe, or crowd events such as New Orleans' Mardi Gras-will have been strongly linked with high subsequent mortality. Omission of relevant controls, such as enplanement measures of numbers of travelers from the most infected foreign origins, can bias the estimated effects for those counties. 11 Alone amongst the above studies in controlling for temperature is Knittel and Ozaltun (2020) , a variable that has been found important in historical patterns of mortality, e.g. Kontis et al. (2020) .

To minimize the effects of omitted variables it is important to test for a comprehensive set of potential initial controls, an important feature of our own methodology. Approaches amongst the above-cited articles differ in the selection of controls, which is often arbitrary, leaving out key controls such as temperature and population density. However, in a large set, many controls may be collinear with other controls or appear insignificant. At least two approaches have been used in this context. The Lasso (least absolute shrinkage and selection operator) regression analysis method aims to enhance the prediction accuracy and interpretability of the resulting statistical model, by requiring the sum of the absolute value of the regression coefficients to be less than a fixed value, which forces certain coefficients to zero, thereby excluding them. Castle et al. (2020) argue that Lasso struggles with negative correlations, 12 and find better performance, from the "general-to-specific" approach implemented in the Autometrics software, which we use to check our regressions. 13 10 See Hardy and Logan (2020) for a comprehensive analysis of the impact of racial and ethnic inequality on COVID-19 mortality, and McLaren (2020) for statistical evidence. 11 Save for Desmet and Waziarg (2021) , none of the above studies corrects for the bias from the differential early onset of the pandemic in some states and later onset in others.

12 This is because negatively correlated variables need to enter jointly as they may not matter much individually. This also proves to be a problem for step-wise regression. 13 The Autometrics algorithms are available in Doornik and Hendry (2018) , see also www.doorn ik.com, the Excel add-in XLModeler, www.xlmod eler.com, and in R (Pretis et al., 2018) .

Our analysis of U.S. state differences in pandemic-related rates of cumulative mortality estimates the effects of racial composition, age structure, poverty, population density, care capacity and other structural features, as well as the timing of the pandemic onset, Spring temperatures (°F) and political allegiance. Across the 51 U.S. states, we find that political allegiance expressed in the way people voted in 2016 had a major effect on mortality outcomes, given the inclusion of the socioeconomic and other controls. This is consistent with spatial studies at the county level, linking partisan allegiance with private attitudes, behavior and COVID-19 deaths. The Desmet and Wacziarg (2021) county-level study of COVID-19 deaths and infection rates in the U.S. established that counties with a high vote-share for the Republicans in 2016 had higher rates of COVID-19 deaths up to the end of November, accounting for population density, racial/ethnic composition and other controls. We confirm this result at the state level for the full year since the arrival of the pandemic when using rates of excess mortality as the dependent variable, as well as for COVID-19 death counts per capita. Our controls also include state interaction effects with the timing of first arrival of the pandemic, implying that the effect of partisanship was even greater in states where the pandemic arrived early.

The paper sets out in Section 2 why excess mortality, expressed as a rate, most accurately captures the impact of the COVID-19 pandemic. Different measures of pandemic outcomes are compared and contrasted, especially in relation to the valid comparability of deaths, case counts, normal deaths, excess deaths and excess mortality across regions, states and countries. Data sources and data quality are assessed, and suggestions are made for improving the transparency and granularity of excess mortality data. Section 3 lays out the conceptual framework and the drivers of excess mortality, and a reduced form empirical model for analyzing cross-state variation in rates of cumulated excess mortality. Section 4 details the data sources, transformations and statistics. In Section 5, the data and empirical results are described for the impact on rates of cumulated excess mortality, and for comparison, of rates of COVID-19 deaths, of state variations in political allegiance and socioeconomic factors in the first 52 weeks of the pandemic. Section 6 concludes.

For country or state comparisons (where the under-recording of pandemic deaths may differ), a robust measure of the count of excess deaths (actual deaths minus "normal" deaths) expressed relative to the population or relative to the benchmark of normal deaths (which we have named the P-score), 14 is greatly to be preferred to simple counts (including per capita) of COVID-19 death rates and infectious case counts, see Table 1 .

This section explains the data quality problems with the raw case and deaths data, it compares and contrasts different measures of excess mortality, and © 2022 International Association for Research in Income and Wealth discusses an alternative measure of the toll of the pandemic, quality-adjusted life expectancy.

Comparisons of excess mortality across regions, states or countries have several purposes. The first is to compare the death toll of the pandemic. The death count of COVID-19, as noted above, suffers from a number of biases, making it an unreliable dependent variable, especially when comparing across countries or states with different definitions of what constitutes a COVID-19 death. Even within the U.S., we noted significant discrepancies between the CDC and JHU sources for COVID-19 deaths, see Figure 1 . Countries with a wide definition for COVID-19 deaths (e.g. Belgium and France) will show that most excess deaths are accounted for by COVID-19, as compared to those with a narrower definition. In the U.S., as Fineberg (2020) observes, counts of deaths from all causes from the National Vital Statistics System (NVSS) 15 are incomplete for recent weeks, and lags may be as long as eight weeks. 16 COVID-19 deaths tend to be under-reported based on the listed causes of death, which reflect varying uncertainty and the judgment of the certifier. For instance, Woolf et al. (2020) find that mortality rates for Alzheimer's disease, dementia and heart disease rose during Spring and Summer pandemic surges, with statistical significance. This could suggest misdiagnosis of a COVID-19 death or that COVID-19 was implicated in these deaths by preventing early treatment. Supporting evidence for the above is from Woolf et al. (2020) who find that COVID-19 deaths were a documented cause of death for 67 percent of excess deaths in the U.S. (1 March to 1 August 2020). Their table shows great variation in the COVID-19 share of excess deaths across the U.S. states, pointing to varying degrees of mismeasurement across states in COVID-implicated mortality, as also implied by our Figure 2 . Figure 1 provided national evidence on the shifting COVID-19 share of excess deaths over time, reflecting improvements in the understanding of the disease, in testing capacity, in diagnosis and other factors. 17 A second reason for making comparisons of excess mortality, to evaluate the effectiveness of policy responses, requires one to dig deeper, and even the simple measures above require further interpretation. Countries or regions may differ in the size of the initial source of infection, in their age structure, in the distribution of co-morbidities in the population and the prevalence of dense urban centers, making some entities more vulnerable.

The third motivation for comparisons is the purely objective one of improving the scientific understanding of the dynamics of the spread of infections, their 15 The U.S. National Center for Health Statistics (NCHS), within the Centers for Disease Control and Prevention (CDC), operates the National Vital Statistics System (NVSS) for the U.S. 16 The lags were longer for North Carolina, as it transitioned from a paper-based to a digital system of recording deaths.

17 Some of the discrepancy between reported COVID-19 deaths and excess deaths could be related to the intensity and timing of increases in testing, and differential guidelines on the recording of deaths that are suspected to be COVID-19 but without a laboratory confirmation; the location of death (hospital, nursing home, or at home) has also affected whether it is recorded as a COVID-19 death .

© 2022 International Association for Research in Income and Wealth incidence and the death rates of those infected. Key to this last endeavor is the production of granular data, i.e. disaggregation of excess deaths data by age, gender, region, and, where possible, socio-economic categories.

Several definitions of the dependent variables capturing pandemic outcomes and used in spatial analyses are summarized and evaluated in Table 1 . These are presented in two groups: measures of COVID-19 deaths, COVID-related deaths and COVID-cases; and measures of excess mortality.

To address the measurement problems inherent in the former group, we argued at an early stage of the pandemic that national statistical offices should publish more granular data and excess mortality P-scores for states and subregions, disaggregated by age, gender and race. 18 The P-score (ratio or percentage of excess deaths relative to normal deaths) is an easily interpretable measure. While many national statistical agencies have published actual weekly deaths and averages of past normal deaths, there were few published benchmarks for more granular or disaggregated data, such as sub-regions or cities. In the U.S., the CDC publishes data on excess deaths and a variant on P-scores (see Table 1 ), defining excess deaths as deviations from normal deaths plus a margin adjusting for the uncertainty around estimated normal deaths. 19 This variant is a lower bound estimate of excess mortality, since the upper 95 percent confidence interval is an upper bound estimate of normal deaths. The variant has the disadvantage that excess mortality data cannot be cumulated over a number of weeks since the margin of uncertainty will narrow as randomness at the weekly level smooths out. These data also cover states but not counties, and are also available disaggregated by gender, age and ethnicity. However, to obtain cross-European or cross-global comparisons in 2020 required data collation from individual national agencies to construct these measures.

Early in the pandemic, separate journalistic endeavors engaged in the timeconsuming effort of collating and presenting more transparent excess mortality data, see Aron and Muellbauer (2020a , Table 1 ). In the intervening year, several agencies have geared up to provide underlying data or present the P-score measures. Perhaps the biggest single pitfall for comparability arises from the accuracy of the raw mortality data. An important drawback of the reported numbers concerns lags in recording and reporting deaths. Countries differ in the efficiency of their death registration systems, particularly where those systems are devolved to regional or local administrations. Problems in one location can affect or delay the national data, and sometimes the national recording system can be slow to absorb regional information. Even in countries with the most sophisticated recording systems, reported mortality lags weeks behind the facts. In a pandemic, it can happen that the capacity of systems is temporarily overwhelmed, most of all in hotspots, often in urban areas. Occasionally the recording methods may be so weak overall, that the observers resort to data on burials. These definitional differences need to be highlighted and made transparent across country data providers and international organizations reporting excess mortality statistics. The period over which comparisons are made needs to be specified carefully, as it is likely that reporting lags are far from uniform across countries.

The Human Mortality Database's Short-term Mortality Fluctuations (STMF) project offers high quality national mortality data by week for 38 countries, and access to the exemplary statistical metafile of HMD. Baseline data cover mainly 2015-2019 (2016 for a few countries), back in many cases to 2000, and disaggregation by several age categories and gender. This provides the raw data from which excess mortality measures can be constructed. Eurostat 20 produce granular mortality data, cross-classified by sex, five-year age-groups and NUTS 3 regional levels within countries for 26 EU member states, EFTA countries and five non-member neighboring countries. They also compile monthly estimates of P-scores using normal deaths defined as the monthly average for 2016 to 2019.

The World Mortality Database has the largest set of countries (94) with a mix of weekly and monthly data. Around half of these come from the above sources, and the rest are directly sourced from national authorities, though some data are of questionable quality. 21 Some of the countries covered by WMD publish data with lags as long as 6 months and even those data may be under-recording deaths in the final weeks of the period covered. Data are presented normalising the excess mortality estimates by the population size, though without evaluating the quality of the underlying population data. 22 Their P-scores (for "all ages" only) use normal deaths based on the previous four to five years of data, where available, using seasonals and annual time trends in regressions to project normal deaths to 2020 and 2021. 23 This is a simplified version of the methods used for instance by the CDC of the U.S., which provides normal seasonally-adjusted baselines on its site. It also differs from the method used by Our World in Data (OWID) which sources data from the above three websites and presents excess mortality statistics (P-scores) for over 100 countries, using an arithmetic average for normal deaths of the years 2015 (or 2016) -2019. OWID disaggregate by several age categories and by gender where feasible, have a discussion of data quality and comparability, and are clearer on the time-frame for their datathey do not use the last few weeks because of recording lags. 20 See webpage: Eurostat excess mortality statistics. https://ec.europa.eu/euros tat/stati stics-expla ined/index.php?title =Excess_morta lity_-_stati stics 21 The dataset is a mixture of reliable and poor-quality data, without discussion of comparative quality. Monthly data are used for countries where weekly data are not available. Availability of weekly data might be considered as indirect indicator of data quality. It is not always the case and there are some exceptions (e.g. Japan doesn't publish weekly data but has high quality data). 22 Notably, a few countries with acceptable mortality quality were excluded from the HMD excess mortality statistics (STMF), mainly because of problematic population estimates (HMD publishes rates). 23 It is not fully clear from the WMD website which countries have data for the full five years for the baseline estimation: 2015-2019. However, if the baseline is estimated for one year of data only, then no trend could be estimated, leading to biased results.

Using the arithmetic average of previous years as the baseline for normal deaths has the advantage of simplicity. However, there are differences in underlying trends in deaths which are likely to be dominated by population growth and the changing age structures of the population, and in other health conditions and their treatment. Ignoring such trends can result in over-or under-estimates of normal deaths, and hence in under-or under-estimates of excess deaths in comparisons between countries or regions. The CDC's estimates of weekly normal deaths at the state level 24 implement the Farrington algorithm, see Noufaily et al. (2012) , which uses over-dispersed Poisson generalized linear models with spline terms to model trends in counts, and accounts for seasonality. The CDC's approach does not take into account evolving state-level population and its age distribution in previous years in modelling normal deaths. Moreover, the Poisson model, designed for small number count data, makes strong assumptions about the underlying stochastic process, which are contradicted by evidence for larger populations, see Aron and Muellbauer (2020b) . Even for the least populous U.S. states, weekly deaths almost never fall below 60, which is not a "small number" in this context. Hence, a better approximation to the data-generating process is likely to be offered by the more flexible ARIMA models. These more flexible ARIMA models have been used at a national level to estimate normal deaths, by Rossen et al. (2021) , Faust et al. (2021) and Shiels et al. (2020) , among others. These authors apply ARIMA models to estimate trends and seasonals from historic data on per capita deaths for different age groups. Estimates of normal deaths for the pandemic period are then made by projecting these trends and seasonals and multiplying up by the current population data for each age group. The pandemic has reduced the population count, especially of older age groups who have high per capita death rates. This method results in lower estimates of normal deaths and higher estimates of excess deaths than a linear projection of past trends which ignores the changing population and age structure. Applying such an approach at the state level would improve the accuracy of excess mortality estimates.

The different measures of excess mortality are compared and contrasted in Table 1 . Assuming that the data definitions for the death counts, such as the definition of the week, type of death count data collected (e.g. registration versus occurrence data) and timeliness of the collection are identical across countries, see Aron and Muellbauer (2020b) , we consider the relative comparability of the statistical measures of excess mortality.

In Figure 3 , the weekly per capita excess deaths and P-scores for the U.S. as a whole are plotted. The P-scores have the advantage that by normalizing relative to normal death counts, they reflect persistent factors affecting normal mortality such as the age composition of the population, the incidence of smoking and air pollution, the prevalence of obesity, poverty and inequality, and the © 2022 International Association for Research in Income and Wealth normal quality of health service delivery. 25 A country like Italy, with an older population, will fare somewhat worse in a per capita excess mortality comparison with countries having younger populations than in a P-score comparison. In a multivariate statistical study, the inclusion of comprehensive controls reduces this advantage of the P-score over a per capita measure of excess mortality, though the P-score reduces the risk of potential bias from unobserved heterogeneity in normal health risks. While P-scores are less affected than per capita excess deaths by differences in the age-composition of the population, they are not immune. Differences in the age distribution between countries would only be irrelevant if mortality risk increased in the same proportion for all. This is not the case because children have a far lower relative mortality risk in the COVID-19 pandemic than under normal conditions. Moreover, differences in urban structure and in population density have relatively little effect on normal mortality rates but have major effects on the spread of a pandemic. P-scores are therefore susceptible to structural differences between countries and regions. However, for temporal comparisons for the same country, their time profile differs little from per capita excess deaths, see Figure 3 .

These themes can be illustrated by comparing rankings of COVID-19 related rates of mortality across U.S. states. Because normal deaths are higher for the elderly and for those with co-morbidities, scaling by normal deaths takes some account of differentials in age composition and socioeconomic characteristics between countries and regions. Indeed, comparing U.S. states, the rankings of states according 25 A possible argument in favor of per capita excess mortality is that total population could be regarded as a rough proxy for the ability of the society to absorb excess deaths. Notes: Several other variables were tried in general initial sets, adopting a general-to-specific approach as a diagnostic tool, see Section 4. to the two metrics are notably different, see Figure 2 . For example, Mississippi had the highest per capita rate of excess mortality in the U.S., while California ranked in the middle of the distribution at number 25. However, on the P-score, California has higher mortality in fifth place while Mississippi is in seventh place. Clearly, normal death rates are far higher in Mississippi than in California. Similar issues affect age-standardized mortality comparisons. The agestandardized mortality rate takes the age-specific mortality rate for each age group, and measures their weighted average using the proportion of the population in the corresponding age groups in a reference population. The same reference population is used in comparing any two countries or regions. While this controls for some of the effects of differences in age structures it neglects the other structural differences affecting pandemic-related mortality in different countries.

An alternative measure is the Z-score compiled by EuroMOMO 26 for 29 states, see Table 1 . The Z-scores standardize data on excess deaths by scaling by the standard deviation of deaths excluding periods of notable excess mortality. The expected value of each country's weekly deaths is estimated using data for the previous five years, taking seasonal factors and trends into account, and adjusting for delays in registration. To fit the baseline, normal variability is measured after excluding seasons leading to excess deaths from additional factors (e.g. Winter influenza and Summer heat waves). Graphic presentation of the Z-scores for different time-periods, countries, and age-groups, with the estimated confidence intervals back to 2015, provides a visual guide to their variability. In contrast to the P-scores, the Z-scores are a less easily interpretable measure. If the natural variability of the weekly data is lower in one country compared to another, for example in larger populations compared with smaller ones, then the Z-scores lead to exaggeration of excess mortality compared to the P-scores. 27 A further disadvantage of Z-scores, compared to P-scores and per capita excess death measures, is that their cumulation over multiple pandemic weeks is problematic. While excess deaths can be cumulated, the standard deviation of normal deaths cannot. EuroMOMO do not reveal the standard deviations used in their calculations. This makes it hard to obtain a comprehensive comparative summary of the pandemic's impact from the Z-scores.

Finally, it should be considered whether excess mortality statistics alone are sufficient to measure the impact of a pandemic. One has to be aware of the limitation of any single measure of comparability between countries. Subsumed within the excess death aggregates are implicit value judgments. For example, crucially in 26 EuroMOMO is a European mortality monitoring entity, aiming to detect and measure excess deaths related to seasonal influenza, pandemics and other public health threats. Official national mortality statistics are provided weekly from the 24 European countries and regions in the EuroMOMO collaborative network, supported by the European Centre for Disease Prevention and Control (ECDC) and the World Health Organization (WHO). https://www.eurom omo.eu/ 27 Given the Poisson model used by EuroMOMO, there should be large differences in Z-scores between countries with different populations even if the P-scores were identical. In practice, because the Poisson is likely to be poor approximation to the stochastic process for the number of deaths, the differences are less pronounced than one would expect, see Appendix in Aron and Muellbauer (2020b) . the case of a pandemic, there is an implicit assumption that the toll of an older life lost is the same as that of a younger life. However, when a younger life is lost, many more years of life expectancy are lost, and one might want to attach a larger weight to deaths of the young.

The health economics literature has given attention to Quality Adjusted Life Expectancy (QALY) as a criterion for expenditure on health-improving policies. QALYs measure the number of reasonably healthy years a person might expect to live. The number of QALYs lost could supplement the increased death count resulting from the pandemic as a measure of its impact. However, detailed actuarial and medical information is entailed in the complex estimation of the number of QALYs lost. QALYs and the attachment of monetary values to QALYs have long been controversial, see Loomes and Mackenzie (1989) , but the concept of a QALY does focus attention on the relative value (by age group) of expected years lost in a pandemic. The excess mortality of working age adults with a normal life expectancy of 30 years might be weighed against the excess mortality of 85-year olds with a life expectancy of 5 years. Attaching more weight to excess mortality for working age adults will affect comparisons of countries with different age-specific mortality rates. Pifarré i Arolas et al.

(2021) estimate years of life lost (YLL) for 81 countries from premature deaths due to COVID-19 based on age-specific life-expectancy tables for each country. For most countries, they based their estimates on COVID-19 death counts, but for a subset of 18 they use excess mortality data. They find that close to half of YLL for all the countries are in the 55 to 75 age group and that only around a quarter of YLL occurred for the over 75s.

To end on a cautionary note, looking only at weekly measures of excess mortality can be slightly misleading. It is important to examine excess mortality in a longer-term perspective too. If, as initially argued, for example, by British statistician, Spiegelhalter (2020), the main impact of COVID-19 is simply to shift forward the date of death by a few months for those close to death because of underlying poor health, then a peak in weekly deaths should be followed by a trough in the following months. 28 Hence the surviving population has a lower weekly expected mortality. For the U.S., Faust et al. (2021) have estimated the impact of so many people dying in the initial wave, that there were fewer vulnerable people as time went on, and proposed a method of adjusting expected counts of deaths downward because of the excess mortality that happened earlier in the year.

Our aim in this paper is to analyze the main factors accounting for cross-state variations in cumulated excess mortality after one year of the pandemic in reduced form models. The papers cited in Section 1 have examined socio-economic drivers © 2022 International Association for Research in Income and Wealth of recorded COVID-19 cases and deaths using county-level cross-section data. A few also examine political drivers of COVID-19 cases and deaths. A major limitation of such studies is the serious measurement biases in reported infections and COVID-attributed deaths, particularly early in the pandemic when testing capacity was often limited, and unequally distributed.

If "all-cause" death registration data are accurate, then excess mortality will not be subject to these measurement biases. However, excess mortality includes the other two components discussed above: avoidable deaths due to non-occurrence of treatments for other causes of ill-health and deaths avoided from shifts in behavior linked with the pandemic. While the peak incidence of COVID-19 deaths occurs 2 to 3 weeks after infection, though with a long tail of later incidence, the timing of the last-mentioned components is likely to be different. The effects of non-treatment of preventable ill-health on mortality include missing early diagnosis and starting cancer treatments later than is advisable, and therefore have mortality consequences likely to materialize months, and in some cases years, later. Similarly, the health damage from the economic disruption caused by the pandemic, especially for lower income people, is likely to affect mortality for years to come.

To interpret the large differences in cumulative COVID-19 death rates among states requires consideration of several factors: the average infection rates in preceding weeks, average mortality risk from COVID-19 and constraints on COVID-specific health capacity, given the prevailing state of knowledge about treatment.

Turning to the first of the factors, consider differences in infection rates. Compare two states with the same average COVID-19 case fatality risk where 1 percent of all adults are infected in A, while 5 percent are infected in B. Then the rate of excess deaths for adults measured by the P-score will be about five times as large in B in the weeks following the incidence of the infection. States that locked down early and had effective test, trace and isolate procedures kept down the average infection rate and hence the excess death rate. Transmission and hence rates of infection are also influenced by factors like the nature of social distancing, availability and use of face masks, and cultural differences in the exercise of self-discipline and following of advice. This set of mitigating factors can be influenced by public policies enacted at state and local levels.

Other factors impacting infection rates include types of occupation, density of living circumstances and proximity to international or cross-state travelers who might import infection. For example, New York's higher excess mortality was influenced by higher initial imports of infections and a higher virus reproduction number given its high density and hard-to-avoid close physical contact on public transport and at work in New York City. States with a higher fraction of adults in multi-generational families, and in locations or occupations (e.g. health workers or taxi-drivers) where the virus can more easily spread, will tend to have higher excess death rates. The influence of the above factors is likely to © 2022 International Association for Research in Income and Wealth evolve over the course of the pandemic as the main sources of infection change and as individual behavior and public policies respond.

The second of the factors mentioned above is mortality risk for infected adults, and this can differ between and within states. The steep age gradient of COVID-19 mortality implies that states with older populations will have higher per capita COVID-19 mortality, other things being equal. The percentage increase in mortality risk may be greater for some ethnic groups, or for some co-morbidities such as diabetes or pre-existing lung conditions which are often correlated with low incomes. Then state differences in ethnic composition, the prevalence of obesity and smoking, and poverty, are likely to influence comparative excess mortality.

Lastly, a state's COVID-19 mortality is increased, and potentially amplified, by limited COVID-specific health capacity. The death rate among infected adults depends on capacity constraints on hospital beds and staff, particularly of nurses with expertise, on ventilators, PPE and on testing and on logistical failures in delivery, e.g. to care homes. Given similar initial capacities, a state with a higher average infection rate will be more likely to run into these constraints. By the same logic, given the same high infection rate, a state with lower health capacity would have a higher rate of excess mortality. This is why there is such a focus on "flattening the pandemic curve." Different capacity constraints can have different implications for different groups. For example, lack of PPE and testing facilities in care homes will have disproportionately larger effects on mortality for the oldest individuals and this could affect state comparisons. However, as these health capacities evolve over time in response to the pandemic, the influence of differences in pre-existing health capacity is likely to decline. Further, the timing of the pandemic's incidence matters also, as medical interventions became more effective with learning about the nature of the virus and its treatment.

The probability of an individual death from COVID-19, P(D), is the product of the probability of being infected, P(I), and the probability of death given infection, P(D/I). Thus, in logs, At the state level, assuming correct measurement of death counts and infection counts, aggregating the individual probabilities yields population proportions of infections and deaths. The log of the state COVID-19 mortality rate is then the sum of two functions, the log of the (lagged) infection rate and the log of the average case fatality rate (CFR) for the population of that state (that is, the proportion of infected people who die from the virus): Equation (2) justifies a log formulation of the empirical equation for the mortality rate. A further reason arises from the highly skewed nature of the levels data, greatly reduced in the log transformation.

The lagged infection rate will be affected by the variables discussed in Section 1, such as population and housing density, the use of public transit, the (1) log P(D) = log P(I ) + log P(D∕I )

(2) log (mortality rate) = log (lagged infection rate) + log (CFR)

© 2022 International Association for Research in Income and Wealth proportion of occupations exposure to early infections arriving from Europe, lock-down and social distancing measures and private behavior responding to the risk of infection and to public measures trying to limit the spread of the virus. The average case fatality rate for the population of that state will vary with factors such as age, race and ethnicity, poverty and inequality, access to good medical care and the capacity of the health system. Our study estimates the cumulative effects over 52 weeks of these influences, which may affect both infection rates and case fatality rates.

We adopt a two-stage model. In the first stage, the time of arrival of a significant level of infection for each state is modelled. In the second stage, rates of excess mortality, measured either per capita or in terms of P-scores, are modelled as a function of the time elapsed from the end of February to the time of arrival of the infection, and of socioeconomic, political, demographic and environmental factors. For comparison, the dependent variable, per capita COVID-19 deaths, is also tested.

A later local onset of the pandemic should have enabled state and local authorities to take advantage of rapidly improving medical knowledge and capacity (the nature of the disease, treatment regimes, testing capacity, and the effectiveness of policies such as social distancing and masks). Private individuals would also have had more time to learn precautionary behavior. Kaplan et al. (2020) use a logistic function in time, a "learning function", to capture the effect of this evolution of behaviors, policies and capacities on health outcomes. We adapt the idea to define a "learning function" that captures the advantage that some states obtained from the later arrival of the virus. The timing of the arrival of the virus in each state is measured by the first day that the 14-day average of daily cases of infection reached, or exceeded, a threshold of 6 cases per 100,000 persons. Our "Timing of onset" function is defined as the inverse of days elapsed from the last day of February to the threshold date (signaling the arrival of serious levels of the virus). The "Timing of onset" function, like the logistic, has the property that the effect is strong at the beginning, but each additional day of delay matters less and less. The inverse function is the dependent variable in the first stage regression estimated in a cross-section regression across states.

Given the probable undercounting of infections in the first wave, it is likely that the dates when the threshold was breached occurred somewhat earlier than indicated in the reported counts. If the bias was uniform across states, it would not matter much. To the extent that the bias varies with socioeconomic differences between states, the interpretation of estimated socioeconomic effects needs to consider the possibility that, in part, these effects may be compensating for measurement bias in the timing measure. If the bias is independent of political allegiance at the state level, it should not affect the estimated effect of political allegiance on excess mortality.

As New York City had the highest initial incidence of the virus, nearness to New York is likely to have been a factor in explaining the timing for other states. Factors such as the degree of urbanization of the state, density of its metropolitan © 2022 International Association for Research in Income and Wealth areas, the use of public transport, and socioeconomic correlates of dense housing conditions are plausible additional candidates for this first stage model of timing.

The second stage consists of a cross-section regression for the 51 U.S. states of the log of cumulated excess mortality on the timing function and on socioeconomic, political, demographic and environmental factors.

As the literature review on more granular spatial differences indicated, prepandemic socioeconomic controls at the state level should include at least the population proportions who are of African American, Hispanic or Asian origin, in the 65+ age group, population density, a measure of health capacity, income and a measure of the incidence of poverty. To these we add the Spring and Autumn temperatures (averaged over March, April and May, and over October to December, respectively) in each state. For excess mortality, very cold weather is likely to induce more influenza and other deaths, as well as increasing COVID-19 deaths by forcing people indoors, where lack of social distancing and inadequate ventilation may increase virus transmission rates. Separating the above into factors affecting the rate of infection vs. those affecting the case fatality rate is typically not possible. For example, if African Americans are more likely to live in crowded housing conditions and work in occupations involving more face-to-face contact, they may suffer higher infection rates. In addition, they may suffer higher case fatality rates, because of pre-existing comorbidities. Similarly, Spring and Autumn temperatures probably affect both the rates of infection and case fatality.

The two-equation model for the 52-week pandemic period may be represented thus:

where EMR is the cumulative excess mortality rate. In equation (3), the inverse function of days elapsed, is explained by a vector of r pre-pandemic structural variables, denoted by Z, where state subscripts have been suppressed. In equation (4), the log of the cumulative rate of excess mortality for the pandemic, EMR 52weeks , is explained by Timing of onset and a second vector of k pre-pandemic structural variables, denoted by X. There can be overlap between the variables in the vectors Z and X, but it is crucial for identification that the Z vector includes some variables not included in X.

The list of relevant variables is by no means exclusive, though there are strong priors based on the evidence from county-level studies. Model selection methods, starting with more general specifications including up to 30 regressors, were used to check for the relevance of the other explanatory variables. Since variation across 51 states is much more limited than across over 3000 counties, sign priors on relevant variables, as well as statistical significance, can help the variable selection process.

For the analysis of cumulative rates of excess mortality in the first 52 weeks of the pandemic, no attempt was made to control for differences in non-pharmaceutical (3)

Timing of onset = g(Z 1 , Z 2 , . . . , Z r )

(4) log EMR 52weeks = f (Timing of onset, X 1 , X 2 , . . . , X k ) © 2022 International Association for Research in Income and Wealth interventions (NPIs) at the state level. State NPIs are endogenous, and likely to be switched on when case-counts and COVID-19 deaths rise strongly. The positive correlation induced would bias estimates of the beneficial effects of NPIs on subsequent excess mortality. In order to measure NPI effects, excess mortality would need to be considered over shorter intervals, with the measures of NPIs lagged to avoid endogeneity bias.

Estimates of excess deaths-defined as the number of persons who have died from all causes, in excess of the expected number of deaths for a given place and time-are from the CDC's National Center for Health Statistics (NCHS), see discussion in Section 2.3. Successive vintages of these estimates reveal surprisingly large revisions in estimates of normal deaths and hence excess deaths. One reason is a switch from historical data for 2016-2019 to data for 2017-2019 in late January 2021, to estimate normal deaths. 29 The longer historical sample is likely to result in less noisy estimates at the state level. We therefore used the CDC estimates of normal deaths based on 2016-2019 up to week 3 of 2021. For weeks 4 to 8 of 2021, the CDC estimates of normal deaths in February 2021 based on 2017-2019 were used. We used the weekly count of excess deaths calculated as observed deaths for that week minus the normal (average expected) number of deaths and cumulate over 52 weeks. For weeks where excess deaths are estimated to be negative, we followed the CDC and use a count of zero. The percentage excess deaths (the P-score) are excess deaths divided by the expected number of deaths. To calculate excess mortality per capita, the excess deaths are divided by 2019 state population (US Census).

Observed death counts are weighted by the CDC to account for incomplete reporting by 51 state jurisdictions in the most recent weeks, and weights are based on completeness of provisional data in the past year as mortality data are recorded with a lag. As we use observed deaths that were recorded over 9 months after the end of the period analyzed, this is not a troubling issue here. In the rare cases where measured weekly excess deaths are negative, we replace such state-level values by zeroes. Hence, in the first weeks of the pandemic, our data on the sum of state-level excess deaths are marginally higher than the national data from the CDC.

We compared two sources of COVID-19 death counts, sourced from the COVID-19 Data Repository by the Center for Systems Science and Engineering (CSSE) at Johns Hopkins University and the U.S. Centers for Disease Control and Prevention (CDC), see 

Studies that capture time variation in the infection and mortality rates note that a later arrival of the virus reduces cumulative COVID-19 attributed mortality. As discussed above, the effect of learning and adaptation gradually fades with time, implying a non-linear function of time elapsed. In place of the logistic function of Kaplan et al. (2020) , we use a simpler function with similar properties: the inverse of the number of days elapsed between the end of February 2020 and the day at which a given case-count threshold was breached. The chosen threshold is the day the 14-day average of new infections exceeded 6 per 100,000. To reduce measurement error, we average case infections from two sources: the CDC and The COVID Tracking Project. The latter, widely-used by other researchers, has a more comprehensive data collection, often giving a higher case count. The inverse days measure is normalised by dividing by its mean.

Except for Desmet and Wacziarg (2021) , none of the studies cited in Section 1 adequately addresses the bias created by arrival of the virus in some states before others, initially largely by the accident of international travel. Dynamic panel studies with the case count as a variable will in principle control for this, as the case count will reflect early incidence. However, this models deaths conditional on infections but does not explain what drives the infections. The case count is endogenous, and when modelled separately, e.g. in a SEM framework, there ought to be a control such as the enplanement measure of Desmet and Wacziarg (2021) linked with travel from high-severity countries, or a learning function as above. Desmet and Wacziarg (2021) use both calendar date and synchronised studies. Greater weight should be accorded to the calendar year results because the synchronised sample results suffer from two problems: sample selection and the mixing up of effects that are likely to vary with time. 31 Simply including the number of days elapsed since the first case (e.g. Liao and Maio (2021) ) fails to capture the nonlinear learning aspect.

In the public health domain, the effects of cold weather on the spread or the severity of the coronavirus have been widely discussed, 32 though less so in the scientific literature. Medical research suggests the virus is more stable at low temperatures. In a study of hospital patients, Kifer et al. (2021) find an association between cold weather and mortality. Even if there were no direct link between cold weather and the virus, cold weather drives people indoors, where aerosol spread is a greater risk factor. 31 Many states had not yet reached the "225 days since onset" criterion that defines the synchronized sample by 30 November, and these states are likely to be systematically different from the others. To illustrate the second issue, a cross-section for the synchronized sample will mix counties at quite different points in the calendar year, so that a like-for-like comparison of the effect of differences in the use of public transit, for example, cannot be made. Transit options in the early days of the pandemic differed, since multiple adaptations of transport use occurred subsequently. 32 Examples are, for the UK, the ONS guidance in ONS (2020a), and for the U.S., the MIT Technology Review. https://www.techn ology review.com/2020/10/08/10096 50/winter-will-make-thepande mic-worse/

Only one of the studies reviewed, Karmakar et al. (2021) , includes temperature as a co-variate. 33 Its omission potentially creates an omitted variable bias since cross-state temperature variations are correlated with other characteristics, for example, the Democrat vote share.

We included Spring and Autumn temperatures in our regressions using data from monthly reports on the larger cities in each state from the National Oceanic and Atmospheric Association (NOAA), National Climate Report. The temperature in °F and the 1981-2020 average temperature in °F were averaged to the state level, and the state-level Spring and Autumn temperatures and deviations from the average were tested in regressions, see Table 2 . Spring is defined to include the months from March to May. Autumn covers October to December.

The first set of potential determinants, see Section 1, includes characteristics of demography, ethnicity and race, health, poverty, income and inequality, education, employment and occupation, commuting and density. With one exception, all covariates in this group retain their original scale and units to assist understanding of the regression coefficients; but the log of median household income is defined as the deviation around the mean value across states.

Since the higher mortality rates for older people and for "Blacks and African Americans" and "Hispanics and Latinos" have been obvious from early in the pandemic, controls for age and ethnicity are common to most (but not all) studies. Following McLaren (2020), we abbreviate the above two racial categories to "African American" and "Hispanic". We also include the proportions reported as "Asian", and "American Indian and Alaska Native". The age distribution (including proportions of the population aged 0-18 years, and older than 65 years) and proportion of the population in racial and ethnic categories were sourced from the United States Census, American Community Survey (ACS) for 2019, see Table 2 . Our general specifications also included the share of multi-generational households, and average family size, from the ACS (in 2019).

Several measures of co-morbidities sourced from the Kaiser Family Foundation (KFF) were tested in the general specifications of our regressions: adults who report smoking, or that they are obese, all in 2019. We also tested uninsured rates for the nonelderly. Categories of vulnerable persons, also from KFF, include numbers of residential nursing home residents as a fraction of the over 65s, and the proportion of incarcerated adults in 2019. Travel measures included in general specifications of our regressions were the percentage of workers 16 years and over who travelled to work by public transportation (excluding taxicab), and the percent of those commuting alone (by car, van or truck), from the 2018 ACS and enplanements in the top 5 airports in each state. 35 Educational variables included the percentage of those over 25 with high school or higher, and also of those over 25 with Bachelor's degree or higher, from the ACS (2019).

Various proximity, density and urbanization variables were examined. To capture closeness to the epicenter of the early outbreak in Wave 1, a weighted New York contiguity dummy was constructed for contiguous states, see Table 2 . This is the product of a dummy equal to 1 for contiguous states, weighted by the log ratio of the New York State's population to the contiguous state's population, since smaller contiguous states are more likely to be disproportionately affected by their populous neighbor. A dummy was included for remote states defined as Hawaii, Alaska, Maine and Washington State. We calculated a standard measure of population density, defined as the 2019 state population per state area in square km, and used the fraction of each state's population living in large cities and a measure of urbanization defined as the fraction of each state's population living in urban areas (2010), both sourced from the U.S. census. A more sophisticated measure of urban density using 2010 Census data is the per square km density of urban areas, see Table 2 and Cox (2016) .

Several authors have emphasized spill-over effects from commuting in dense Metropolitan Areas, spanning states. We calculated a weighted Metropolitan Statistical Area (MSA) density measure that takes some account of population density in populous overlapping MSAs as follows. Using the 2010 Census state population figures to match the 2010 Census MSA population figures, we calculated first, the actual population of the MSA as a share of the state population. Second, we calculated the average MSA density as the MSA actual population divided by the MSA occupied land area. The product of these two is the density of the MSA weighted by the share of MSA population in the state, and it was scaled by 1000. We use a cut-off point for MSAs of populations over 1.5m in 2010. The MSA occupied land area is approximated by multiplying the total MSA land area by the MSA share of state population. This was an elaborate exercise as some MSAs are shared with other states, so that it is required to apportion the part of each shared MSA that belongs to each state. The measure is zero for states in which no MSA's population exceeded 1.5 million.

A second set of potential determinants concern health care capacity, reflected in the availability of PPE, numbers of ICU beds and ventilators, preventive and pre-hospital care, numbers of doctors and critical care nurses, laboratory networks and testing and contact tracing infrastructure. Several measures were sourced from the KFF including the numbers of ICU beds per 10,000 population, of hospital beds per 1000 population, and of critical care nurses per 10,000 adults.

Recent literature adds political partisanship in the U.S. to the subset of drivers of pandemic mortality, which helps to capture private attitudes and behavior, see Section 1. The hypothesis is that partisanship influences "compliance" with state-level safety measures that mitigate transmission of infection, coupled with voluntary behavior to reduce vulnerability. Our measure of partisanship is the Democrat share of the popular vote received in each State in the 2016 Presidential General Election, sourced from the Federal Election Commission of the U.S., Federal Election Commission (2017), Appendix A. We also included the political affiliation of the Governorship for each state as at 2020, sourced from KFF.

Interaction effects were defined between the "Timing of onset", and the Democrat vote share and log median household income, all taken as deviations from their means, see Section 5 for discussion.

The two-equation model of Section 3.2, represented in equations (3) and (4), was applied across 51 U.S. states (including Washington, D.C.) using two-stage least squares (2SLS) and OLS. Table 2 provides definitions and sources for the data. The "Timing of onset" function corresponding to equation (3) was estimated in a first stage, see Section 4.2 and Table 2 for the definition of the dependent variable. The chosen specification is the result of the reduction from a more general to a parsimonious formulation, on plausible correlates of early arrival of infections. The fitted value was used as an instrument in estimating the second-stage regression of the equation for the log of cumulative per capita excess mortality. This helps address the probable endogeneity of the timing of the pandemic's arrival in each state.

The "Timing of onset" function has its highest value for New York, clearly the first state to be seriously affected, followed by New Jersey, Michigan, Vermont, Louisiana, Massachusetts, and Connecticut. Those states hit early had a double disadvantage: a longer period for deaths due to the pandemic to cumulate and less time to benefit from learning about appropriate public and private behavioral and medical responses.

The estimated first-stage equation is shown in Table 3 . The early arrival of the pandemic is explained by three geographical measures, the percentage of the © 2022 International Association for Research in Income and Wealth population who are African American, median household income and the Spring temperature. A lower median income and a lower Spring temperature are associated with the case-count threshold being breached earlier. The geographical measures are a measure of nearness to New York state for the contiguous states (zero for the non-contiguous states), a measure of population density for the metropolitan areas in each state and an index of urbanization. Density and nearness to New York state are associated with the earlier arrival of the pandemic.

The dependent variable for the second equation in the model, i.e. corresponding to equation (4), is the log of the per capita cumulative excess mortality rate, EMR, for 52 weeks. Similar models are estimated for the log P-score and log per capita COVID-19 deaths, see Table 4 . The first column of results in Table 4 shows the crude correlation, controlling only of the remoteness dummy, between log EMR and the Democrat vote share. The estimated second-stage equation for log EMR, using two-stage least squares, is shown in column 2, followed by the OLS estimates in column 3. The estimates in these two columns are fairly close, despite probable endogeneity bias. Columns 5 and 7 show 2SLS estimates for, respectively, the log P-score and log per capita COVID-19 deaths as the dependent variables (the corresponding crude correlations are shown in columns 4 and 6).

Several controls are common to the majority of studies cited in Section 1: measures of density and urban structure, measures of race and ethnicity, the age structure, poverty and income Given the widespread discussion of temperature and our prior that states where the pandemic arrived first suffered a serious disadvantage, this suggested a basic set of 13 controls plus an intercept, including three geographic measures: remoteness, state population density and urban density. We also controlled for two interaction effects, the first between "Timing of onset" and the Democrat vote share, and the second between the "Timing of onset" and log median household income. The former effect would capture increasingly cautious behaviors by Democrat voters that mattered more for mortality when the risks were particularly pronounced, as in those states hit hardest early on. Given the pandemic was seeded by the arrival of fairly affluent travelers from Europe, the latter interaction effect would suggest a positive link with states that had higher average incomes. Desmet and Wazciarg (2021) find that the early positive correlation Notes: Stars indicate significance levels: ***P-value lower than 0.01, **P-value between 0.01 and 0.05, *P-value between 0.05 and 0.1. All variables are defined in Table 2 Notes: Stars indicate significance levels: ***P-value lower than 0.01, **P-value between 0.01 and 0.05, *P-value between 0.05 and 0.1. In the interaction effects, variables are expressed as a deviation from their means. All variables are defined in Table 2 .

© 2022 International Association for Research in Income and Wealth between COVID-19 mortality and income switches to a negative correlation as the pandemic progressed. This might suggest that early arrival states, where the "Timing of onset" is above average, would experience a positive income effect, while late arrival states would have a negative income effect. Other controls were discussed in Section 4, and included the proportion of workers using public transit, the proportion of those aged under 65 without health insurance, the ratio of nursing home residents to the population aged 65 or above, and 20 other variables. The Autometrics software of Doornik and Hendry (2018) has the option of searching over a broad set of other controls in a general-to-specific reduction, given the retention of a basic set of key controls. The software was used to check that none of these other controls was statistically relevant, confirming the parsimonious specification shown in columns 2 and 3. A non-nested test, see Aneuryn-Evans and Deaton (1980) , strongly supports the log version of the dependent variable versus the linear alternative: the log of the fitted value from the linear version of the equation is insignificant when added to the log specification as shown in columns 2 or 3. However, adding the exponential of the fitted value from the log version to the linear version gives a highly significant result, implying that the linear version is seriously mis-specified. Replacing the 2016 Democrat vote share by the equivalent 2020 vote share, makes little difference to the results, with a slightly lower (negative) coefficient on the Democrat vote share.

The robustness of the findings for log per capita excess mortality is demonstrated in Table 5 by, in turn, dropping the first 10 observations, the second 10, and so on, to the last 10 observations. This demonstrates the relative stability of the coefficients for the Democrat vote-share and its interaction with the "Timing of onset", for the Democrat Governor dummy, and the proportions of African Americans and Hispanics. For all the other parameter estimates for the regressions with omitted states (not shown), the 95 percent confidence intervals include the point estimates from the full sample. The implication is that the results are clearly not driven by outliers concentrated in a few states and are fairly insensitive to the exclusion of particular states.

Comparing coefficients in Table 4 for the log P-score measure as dependent variable with those for the specification with log per capita excess mortality, shows a slightly lower (negative) coefficient on the Democrat vote share, and somewhat lower coefficients on the percentage of poor residents, population density and Spring temperature. It is striking that the effect of age composition disappears entirely (the t-ratio is 0.2, and the variable was omitted). As the P-score measures excess deaths relatively to normal deaths, it already captures some differences in mortality due to pre-existing co-morbidities, of which age is the most important. The effects of race and ethnicity are broadly similar for the per capita excess mortality and P-score measures. By the same token, this suggests that the effects of race and ethnicity are not related to the higher, pre-pandemic mortality rates of minority populations. Table 4 for the full set of variables included in the regressions). Stars indicate significance levels: ***P-value lower than 0.01, **P-value between 0.01 and 0.05, *P-value between 0.05 and 0.1. In the interaction effects, variables are expressed as a deviation from their means. All variables are defined in Table 2 .

These findings have implications when comparing the P-score statistics across states and countries. While, for simple comparisons, the P-score is probably the best statistical measure, and preferable to per capita measures, even for the P-score, structural socioeconomic and environmental differences need to be taken into account. In other words, P-scores do not fully capture the differences in racial and ethnic composition, and in poverty and urban density, despite being normalised against normal deaths. Thus, unqualified comparisons of per capita excess deaths, and even of the preferred P-score measure, should not be used to assess the relative performance of public policy in different locations.

Given alternative sources of COVID-19 death counts in the U.S., a comparison was made to select the more robust measure on the basis of whether there is mis-measurement against the excess deaths measure. In time series regressions of aggregate U.S. data of log per capita COVID-19 deaths on log per capita excess deaths, the R 2 is higher and the standard error lower for CDC data than for JHU data, whether or not the first few weeks of the pandemic are included. In crossstate regressions of the 52-week cumulative per capita data, the same conclusion is reached. Even though excess deaths also include spill-overs in deaths from conditions untreated because health systems were overwhelmed, over a 52-week period and cross-state variation, one would not expect such spill-overs to substantially bias the relationship between true COVID-19 death counts and excess deaths. We therefore concluded that the CDC COVID-19 death count is less inaccurate than the JHU data.

There are striking differences in the state rankings by per capita excess mortality versus the rankings by per capita COVID-19 deaths, see Figure 2 and Section 2. Thus, it is somewhat surprising that the estimates in columns 2 and 7 of Table 4 are not more different. For the per capita COVID-19 deaths measure, the effects of the Democrat vote share and the Democrat Governor effect are, respectively, a little stronger, and weaker; the timing effect is slightly stronger; and the proportions of African Americans and Hispanics have somewhat stronger effects, though prove less significant for Asians. The interaction effects with the timing of the pandemic are even stronger for the COVID-19 measure than for the two excess mortality rate measures. However, consistent with substantial measurement errors in the dependent variable, the equation fit for the COVID-19 specification is far worse with the equation standard errors measuring over 60 percent higher.

The literature cited in Section 1 on the role of partisanship in the pandemic, explored the links between the rates of COVID-19 infections and deaths and political attitudes and beliefs, reflected in private behaviors such as maskwearing and social distancing and compliance with official advice and mandates. The Democrat vote share can be interpreted as a proxy for such private behaviors, when controlling for both the differential onset across states of severe outbreaks and the different risk groups. This interpretation accords well with © 2022 International Association for Research in Income and Wealth the findings at county-level of Desmet and Wacziarg (2021) and Gollwitzer et al. (2020) .

As explained in Section 3, the cross-section equations presented in Table 4 are reduced-form equations which mix the effects governing infection rates, those governing mortality (given infection), and the pandemic's indirect effects on other types of deaths. For example, the coefficient on the proportion of African Americans in the population may be connected with higher infection rates in states with higher proportions of African Americans, as well as with their higher case-fatality rate. On the face of it, the estimated coefficient of 2.11 in Table 4 column 2, implies that a 1 percent shift in the population from White to African American results in a 2.11 percent increase in excess mortality. However, this cannot be given a strict interpretation of individual mortality risk faced by an African American person, even given the other controls in our regression (including poverty, political allegiance, population density and the age distribution). It might be that states with high proportions of African Americans have other characteristics, not controlled for, raising mortality risk.

No studies of which we are aware control for differences in wealth between African American and other households, and, as Hardy and Logan (2020) point out, wealth inequality between African Americans and Whites is far greater than earnings inequality. It is plausible that accurate controls for wealth, educational quality, family composition and discrimination (e.g. in labor, housing and credit markets), would greatly reduce and perhaps eliminate racial differences in excess mortality rates.

Our racial-ethnic estimates are broadly in line with those of county-level studies of COVID-19 mortality rates. County-level measures for the effects of variations in the proportion of African Americans, with Whites as the reference group, typically vary in a range from about 1.5 to 3, according to other controls included and the period covered, e.g. McClaren (2020) . Similarly, the effect of variations in the proportion of Hispanics, at somewhat over half of the effect for African Americans, is also not far from county-level estimates. The coefficient on the proportion of Asians is similar to that for African Americans but much less precisely estimated. 36 An important role is played by the inclusion of partisanship for the estimates of racial and ethnic disparities. The Democrat vote share effect is highly significant and robust to the exclusion of ten states at a time from the cross-section regressions for COVID-19 related mortality. As racial and ethnic minorities tend to vote disproportionately for the Democratic Party, their population shares are strongly positively correlated with the Democrat vote share, which has a negative effect on excess mortality. Therefore, if the Democrat vote share was omitted from the cross-state regression, this would result in a downward omitted variable bias on the coefficients for the population shares of African Americans and Hispanics. Indeed, 36 Rossen et al. (2020) estimate normal deaths by age and racial group at the national level. They report disparities in excess mortality incidence rates in 2020 for different age groups and races. The rate per 100,000 in the 65+ age group for African Americans and Hispanics is just over double that for Whites; for the 25-64 age group, the African American rate is 2.6 times that of Whites, and for Hispanics it is 1.9 times that of Whites. For those of Asian descent, the rates are similar to those of Whites.

© 2022 International Association for Research in Income and Wealth the omission almost halves the estimated coefficients for African Americans and Hispanics, with a substantial loss of precision (these results are not reported in Table 4 ).

The coefficient of 4.4 on the percentage of residents aged 65 or more is consistent with the steep age gradient of COVID-19 mortality and the fact that hardly any deaths occur for those under 18. The estimated coefficient of 7.0 on the percent classified as poor, though broadly consistent with studies showing strong links between economic deprivation and COVID-19 mortality, cannot be taken too literally. On the face of it, it implies that a 1 percent of population increase in those below the poverty line, implying a 1 percent decrease in those above, results in 7.0 percent increase in excess mortality. The figure is surprisingly high given that the percentages of African American and Hispanic residents are also controlled for, and poverty rates for these groups are above average. It is likely that being classified as poor is associated with other unobserved characteristics that raise mortality risk. 37 The positive interaction effect between the timing of onset of the pandemic and median income in a cross-state regression, given controls for race, ethnicity and poverty, likely reflects the fact that many of those who first seeded the infection in the U.S. were affluent travellers returning from Europe. It implies a negative effect of higher incomes on mortality in the states with a later onset of the pandemic. This could be related to the ability of the affluent to afford good medical care and avoid close contacts that raise infection risk.

Differences in state population density (measured as population per square km) and in urban density have the expected effects, consistent with the great majority of granular studies cited in Section 1. Through the "Timing of onset" function, there is an additional effect from density measured for the MSAs to which each state belongs as well as a measure of urbanization and a control for bordering on New York state. The estimated effect for Spring temperature, measured in degrees Fahrenheit, suggests that a one-degree higher average temperature is associated with a 2 percent lower rate of excess mortality for the full period of 52 weeks. Even if there were no direct link between cold weather and the virus, the fact that cold weather drives people indoors, where aerosol spread is a risk factor, is widely suspected of association with excess mortality. Some studies of historical patterns of mortality, e.g. Kontis et al. (2020) , find significant temperature effects where low Spring temperatures and high Summer temperatures are associated with higher death rates. As the CDC does not use temperature controls to estimate normal death rates, part of what our temperature effect captures could be the higher mortality that would have occurred even without the pandemic.

For the full 52 weeks of the pandemic analyzed, the bilateral correlation is close to zero between any of the three COVID-related mortality measures © 2022 International Association for Research in Income and Wealth and the 2016 Democrat vote share. Given the inclusion of a set of plausible controls, however, those states with higher Democrat vote shares, experienced lower COVID-related mortality on all three mortality measures. This finding parallels the evidence at a county-level for data to the end of November 2020 from Desmet and Wacziarg (2021) . The finding is consistent with the more cautious and better-informed behavior by Democrat voters on the 2016 election measure. Moreover, the interaction effects suggest the negative Democrat vote share effect on mortality was even greater in states where the infection arrived early. If the Democrat vote share is omitted, this results in an under-estimation of the estimated disparities in excess mortality suffered by African Americans and Hispanics.

This paper is the first state-level, spatial analysis of excess mortality across the 51 US states (including Washington, D.C.), showing for the full year since the arrival of the pandemic in the U.S., the effects of racial composition, age structure, poverty, income, the timing of the pandemic onset, temperature, population density and other structural features, and political partisanship. We have focused on two excess mortality measures in a log formulation: per capita excess mortality and the P-score (excess deaths relative to normal deaths). Analyzing the drivers of excess mortality measures, rather than counts of COVID-19 deaths as typically used in epidemiological studies, avoids the well-documented mismeasurement biases from under-reported pandemic-related cases and deaths. Our paper has clarified definitions and data measurement issues around excess mortality, considering data quality and comparability both internationally and within the U.S.

A reduced form empirical specification was derived from the theoretical link between the mortality rate and lagged infection rates and average case fatality rates. A log-linear formulation captured a mixture of the influences on infection rates and case fatality rates with co-variates common to granular studies of COVID-19 per capita death and infection counts. Unlike in most cross-section studies, the selection of relevant regressors was not ad hoc, or based on bilateral correlations, but tested against a general-to-specific econometric analysis from a wide range of initial controls. This set included important socioeconomic regressors, temperature, the timing of the onset of the pandemic, and interaction effects to capture plausible non-linearities, each rarely included in published studies. Our two-stage approach modelled first, the timing of the pandemic across states, and then, using two-stage least squares, the second stage models for log excess mortality rates. This helped avoid the endemic problem found in almost all the studies we have cited, save for Desmet and Waziarg (2021) , of a serious omitted variable bias from the differential arrival in time of the pandemic across states. Non-nested tests confirmed that the log formulation is far superior to the additive linear formulation used by many studies to model per capita COVID-19 deaths. The latter formulation is a serious mis-specification given that the theory supports an additive formulation in logs. In general, our © 2022 International Association for Research in Income and Wealth study has tried to avoid empirical shortcomings from inappropriate choice of functional form, the exclusion of key controls, and selection and measurement biases.

The inclusion of political partisanship adds a key omitted variable to the more usual regressors, which are focused on the characteristics affecting transmission risk and vulnerability to infection and the preparedness and capacity of the public health and social care systems. We find that states with higher Democrat vote shares experienced lower excess mortality rates, controlling for a broad set of underlying risk factors. This suggests more cautious behaviors by those voting Democrat in the 2016 election. These findings, linking partisan differences to mortality outcomes in the pandemic, are consistent with recent studies that clarify the impact of partisanship on actual behavior. Moreover, the interaction effects in our model suggest that the effect of Democrat voting (in 2016) in reducing mortality was even greater in states where the infection arrived early. Our findings parallel the evidence at a county-level for data to the end of November 2020 from Desmet and Wacziarg (2021) , but such interaction effects have not been considered in any county-level cross-section studies of COVID-19 deaths. Mostly, this literature has not taken Spring temperatures into account. Low Spring temperatures increased COVID-related mortality. The absence of interaction effects and the finding that Spring temperatures tend to be lower in states with larger Democrat vote shares, implies that previous estimates of the effect of partisanship on COVID-19 deaths may have under-estimated the mortality-reducing effect of the Democrat vote share.

A striking implication of our findings is that the failure in many spatial county-level or state-level studies to control for the effect of political partisanship on COVID-related mortality probably caused a downward omitted variable bias of the disparities associated with being African American and Hispanic, and hence under-estimated the effects of race. This is the consequence of a positive correlation between minority population shares and the Democrat vote share, but a negative correlation between the Democrat vote share and COVIDrelated mortality.

No attempt was made to control for differences in non-pharmaceutical interventions (NPIs) at the state level for cumulative rates of excess mortality in the 52week period, as NPIs are likely to be switched on when case-counts and COVID-19 deaths rise strongly. To measure such effects, excess mortality would need to be considered over shorter intervals, and the measures of NPIs, see Hale et al. (2021) , lagged to avoid endogeneity bias.

The robustness of our analysis was demonstrated in Section 5.5. We also compared models for the two dependent excess mortality variables (i.e. per capita excess deaths and the P-score). The rankings of U.S. states according to the per capita and P-score measures of excess mortality are notably different, see Section 2. Despite the differences, the cross-section models of state differences for the two excess mortality measures find similar strong effects for partisanship and broadly similar interpretations for the socioeconomic variables. The P-score is the preferred measure for simple cross-country comparisons since it is scaled by normal deaths (taking some account of differentials in age composition and socioeconomic characteristics), but inclusion of comprehensive controls in a multivariate © 2022 International Association for Research in Income and Wealth statistical study reduces this advantage over the per capita measure of excess mortality. As might be expected, age drops out in models for the P-score, but it is an important control in models for per capita excess mortality. It is striking that there are equally strong racial and ethnic effects for the P-score. These go beyond what is captured in the pre-pandemic normal deaths, suggesting levels of discrimination and disadvantage during the pandemic well above those previously prevailing.

Repeating the analysis with the log of COVID-19 deaths per capita measure as the dependent variable finds a similarly strong political effect, and similar socioeconomic controls mattering, but the equation fit is substantially worse than for excess deaths per capita (the fit is worse still when using the JHU-sourced COVID-19 death count). All the cross-state evidence, consistent with the literature cited in the introduction, confirms that political allegiance appears to have a major effect on beliefs and on behavior in the politically polarised US. This polarisation is one of the reasons for the national failure of the US in responding to the pandemic, as documented by Kinsella et al. (2020) and Altman (2020) .

Our findings have implications for further research on more granular data. Currently, the U.S. CDC does not produce estimates of weekly excess deaths down to the county level. Such data can be very noisy for counties with small populations. Moving to a monthly or even quarterly frequency would ameliorate this problem and make more granular analysis possible. We also suggest that, at the state level, the CDC control for changes in population and age composition for improved estimates of normal and hence excess deaths.

To make simple comparisons of pandemic-related rates of mortality across countries and states to evaluate public policy choices, our findings suggest that the P-score measure is preferable to per capita excess mortality, but is far from immune to structural differences between countries. The timing of the pandemic, poverty, racial and ethnic composition, occupational structure and the nature of urban density all need to be taken into account in gauging the success or otherwise of public policies in different locations. International comparability is more difficult in these dimensions, given problems with standardizing categories in measures of deprivation, occupational classification (sometimes not recorded on death certificates, but recoverable from census records) and missing data for some countries on the sensitive issue of ethnicity. The international NUTS classification of regions 38 provides a possible comparable frame for international comparisons. As regions differ in their urban/rural structure, comparing regional data can give important insights into risk factors for death rates. Moreover, as the incidence of the pandemic differs in timing and intensity, regional comparisons can throw light on the dynamics of the spread of infections. 

© 2022 International Association for Research in Income and Wealth

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