Sam Watson’s journal round-up for 27th May 2019

Every Monday our authors provide a round-up of some of the most recently published peer reviewed articles from the field. We don’t cover everything, or even what’s most important – just a few papers that have interested the author. Visit our Resources page for links to more journals or follow the HealthEconBot. If you’d like to write one of our weekly journal round-ups, get in touch.

Spatial interdependence and instrumental variable models. Political Science Research and Methods Published 30th January 2019

Things that are closer to one another are more like one another. This could be the mantra of spatial statistics and econometrics. Countries, people, health outcomes, plants, and so forth can all display some form of spatial correlation. Ignoring these dependencies can have important consequences for model-based data analysis, but what those consequences are depend on how we conceive of the data generating process and model we therefore use. Spatial econometrics and geostatistics both deal with the same kind of empirical problem but do it in different ways. To illustrate this consider an outcome y = [y_1,...,y_n]', for some units (e.g. people, countries, etc.) i at locations l = [l_1,...,l_n]' in some area A \in \mathbb(R)^2. We are interested in the effect of some variable x. The spatial econometric approach is typically to consider that the outcome is “simultaneously” determined along with its neighbours:

y = \beta x + Wy + u

where W is a “connectivity” matrix typically indicating which units are neighbours of one another, and u is a vector of random error terms. If the spatial correlation is ignored then the error term would become v= Wy + u, which would cause the OLS estimator to be biased since x would be correlated with v because of the presence of y.

Contrast this to the model-based geostatistical approach. We assume that there is some underlying, unobserved process S(l) from which we make observations with error:

y = \beta x + S(l) + e

Normally we would model S as a zero-mean Gaussian process, which we’ve described in a previous blog post. As a result, if we don’t condition on S the y are mulivariate-normally distributed, y|x \sim MVN(\beta x, \Sigma). Under this model, OLS is not biased but it is inefficient since our effective sample size is n(tr(\Sigma))/\mathbf{1}^T\Sigma \mathbf{1}, which is less than n.

Another consequence of the spatial econometric model is that an instrumental variable estimator is also biased, particularly if the instrument is also spatially correlated. This article discusses the “spatial 2-stage least squares” estimator, which essentially requires an instrument for both x and Wy. This latter instrument can simply be Wx. The article explores this by re-estimating the models of the well-known paper Revisiting the Resource Curse: Natural Disasters, the Price of Oil, and Democracy.

The spatial econometric approach clearly has limitations compared to the geostatistical approach. The matrix W has to be pre-specified rather than estimated from the data and is usually limited to just allowing a constant correlation between direct neighbours. It would also be very tricky to interpolate outcomes at new places, and also is rarely used to deal with spatially continuous phenomena. However, its simplicity allows for these instrumental variable approaches to be used more simply for estimating average causal effects. Development of causal models within the geostatistical model framework is still an ongoing research question (of mine!).

Methodological challenges when studying distance to care as an exposure in health research. American Journal of Epidemiology [PubMed] Published 20th May 2019

If you read academic articles when you are sufficiently tired, what you think the authors are writing may start to drift from what they are actually writing. I must confess that this is what has happened to me with this article. I spent a good while debating in my head what the authors were saying about using distance to care as an instrument for exposure in health research rather than distance as an exposure itself. Unfortunately, the latter is not nearly as interesting a discussion for me as the former, but given I have run out of time to find another article I’ll try to weave together the two.

Distance is a very strong determinant of which health services, if any, somebody uses. In a place like the UK it may determine which clinic or hospital of many a patient will attend. In poorer settings it may determine whether a patient seeks health care at all. There is thus interest in understanding how distance affects use of services. This article provides a concise discussion of why the causal effect of distance might not be identified in a simple model. For example, observation of a patient depends on their attendance and hence distance so inducing selection bias in our study. The distance from a facility may also be associated with other key determinants like socioeconomic status introducing further confounding. And finally distance can be measured with some error. These issues are illustrated with maternity care in Botswana.

Since distance is such a strong determinant of health service use, it is also widely used as an instrumental variable for use. My very first published paper used it. So the question now to ask is, how do the above-mentioned issues with distance affect its use as an instrument? For the question of selection bias, it depends on the selection mechanism. Consider the standard causal model shown above, where Y is the outcome, X the treatment, Z the instrument, and U the unobserved variable. If selection depends only on Z and/or U then the instrumental variables estimator is unbiased, whereas i selection depends on Y and/or X then it is biased. If distance is correlated with some other factor that also influences Y then it is no longer a valid instrument if we don’t condition on that factor. The typical criticism of distance as an instrument is that it is associated with socioeconomic status. In UK-based studies, we might condition on some deprivation index, like the Index of Multiple Deprivation. But, these indices are not that precise and are averaged across small areas; there is still likely to be heterogeneity in status within areas. It is not possible to say what the extent of this potential bias is, but it could be substantial. Finally, if distance is measured with error then the instrumental variables estimator will be biased (probably).

This concise discussion was mainly about a paper that doesn’t actually exist. But I think it highlights that actually there is a lot to say about distance as an instrument and its potential weaknesses; the imagined paper could certainly materialise. Indeed, in a systematic review of instrumental variable analyses of health service access and use, in which most studies use distance to facility, only a tiny proportion of studies actually consider that distance might be confounded with unobserved variables.

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Sam Watson’s journal round-up for 12th November 2018

Every Monday our authors provide a round-up of some of the most recently published peer reviewed articles from the field. We don’t cover everything, or even what’s most important – just a few papers that have interested the author. Visit our Resources page for links to more journals or follow the HealthEconBot. If you’d like to write one of our weekly journal round-ups, get in touch.

Estimating health opportunity costs in low-income and middle-income countries: a novel approach and evidence from cross-country data. BMJ Global Health. Published November 2017.

The relationship between health care expenditure and population health outcomes is a topic that comes up often on this blog. Understanding how population health changes in response to increases or decreases in the health system budget is a reasonable way to set a cost-effectiveness threshold. Purchasing things above this threshold will, on average, displace activity with greater benefits. But identifying this effect is hard. Commonly papers use some kind of instrumental variable method to try to get at the causal effect with aggregate, say country-level, data. These instruments, though, can be controversial. Years ago I tried to articulate why I thought using socio-economic variables as instruments was inappropriate. I also wrote a short paper a few years ago, which remains unpublished, that used international commodity price indexes as an instrument for health spending in Sub-Saharan Africa, where commodity exports are a big driver of national income. This was rejected from a journal because of the choice of instruments. Commodity prices may well influence other things in the country that can influence population health. And a similar critique could be made of this article here, which uses consumption:investment ratios and military expenditure in neighbouring countries as instruments for national health expenditure in low and middle income countries.

I remain unconvinced by these instruments. The paper doesn’t present validity checks on them, which is forgiveable given medical journal word limitations, but does mean it is hard to assess. In any case, consumption:investment ratios change in line with the general macroeconomy – in an economic downturn this should change (assuming savings = investment) as people switch from consumption to investment. There are a multitude of pathways through which this will affect health. Similarly, neighbouring military expenditure would act by displacing own-country health expenditure towards military expenditure. But for many regions of the world, there has been little conflict between neighbours in recent years. And at the very least there would be a lag on this effect. Indeed, in all the models of health expenditure and population health outcomes I’ve seen, barely a handful take into account dynamic effects.

Now, I don’t mean to let the perfect be the enemy of the good. I would never have suggested this paper should not be published as it is, at the very least, important for the discussion of health care expenditure and cost-effectiveness. But I don’t feel there is strong enough evidence to accept these as causal estimates. I would even be willing to go as far to say that any mechanism that affects health care expenditure is likely to affect population health by some other means, since health expenditure is typically decided in the context of the broader public sector budget. That’s without considering what happens with private expenditure on health.

Strategic Patient Discharge: The Case of Long-Term Care Hospitals. American Economic Review. [RePEcPublished November 2018.

An important contribution of health economics has been to undermine people’s trust that doctors act in their best interest. Perhaps that’s a little facetious, nevertheless there has been ample demonstration that health care providers will often act in their own self-interest. Often this is due to trying to maximise revenue by gaming reimbursement schemes, but also includes things like doctors acting differently near the end of their shift so they can go home on time. So when I describe a particular reimbursement scheme that Medicare in the US uses, I don’t think there’ll be any doubt about the results of this study of it.

In the US, long-term acute care hospitals (LTCHs) specialise in treating patients with chronic care needs who require extended inpatient stays. Medicare reimbursement typically works on a fixed rate for each of many diagnostic related groups (DRGs), but given the longer and more complex care needs in LTCHs, they get a higher tariff. To discourage admitting patients purely to get higher levels of reimbursement, the bulk of the payment only kicks in after a certain length of stay. Like I said – you can guess what happened.

This article shows 26% of patients are discharged in the three days after the length of stay threshold compared to just 7% in the three days prior. This pattern is most strongly observed in discharges to home, and is not present in patients who die. But this may still be just by chance that the threshold and these discharges coincide. Fortunately for the authors the thresholds differ between DRGs and even move around within a DRG over time in a way that appears unrelated to actual patient health. They therefore estimate a set of decision models for patient discharge to try to estimate the effect of different reimbursement policies.

Estimating misreporting in condom use and its determinants among sex workers: Evidence from the list randomisation method. Health Economics. Published November 2018.

Working on health and health care research, especially if you conduct surveys, means you often want to ask people about sensitive topics. These could include sex and sexuality, bodily function, mood, or other ailments. For example, I work a fair bit on sanitation, where frequently self-reported diarrhoea in under fives (reported by the mother that is) is the primary outcome. This could be poorly reported particularly if an intervention includes any kind of educational component that suggests it could be the mother’s fault for, say, not washing her hands, if the child gets diarrhoea. This article looks at condom use among female sex workers in Senegal, another potentially sensitive topic, since unprotected sex is seen as risky. To try and get at the true prevalence of condom use, the authors use a ‘list randomisation’ method. This randomises survey participants to two sets of questions: a set of non-sensitive statements, or the same set of statements with the sensitive question thrown in. All respondents have to do is report the number of the statements they agree with. This means it is generally not possible to distinguish the response to the sensitive question, but the difference in average number of statements reported between the two groups gives an unbiased estimator for the population proportion. Neat, huh? Ultimately the authors report an estimate of 80% of sex workers using condoms, which compares to the 97% who said they used a condom when asked directly.

 

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Sam Watson’s journal round-up for 16th April 2018

Every Monday our authors provide a round-up of some of the most recently published peer reviewed articles from the field. We don’t cover everything, or even what’s most important – just a few papers that have interested the author. Visit our Resources page for links to more journals or follow the HealthEconBot. If you’d like to write one of our weekly journal round-ups, get in touch.

The impact of NHS expenditure on health outcomes in England: alternative approaches to identification in all‐cause and disease specific models of mortality. Health Economics [PubMedPublished 2nd April 2018

Studies looking at the relationship between health care expenditure and patient outcomes have exploded in popularity. A recent systematic review identified 65 studies by 2014 on the topic – and recent experience from these journal round-ups suggests this number has increased significantly since then. The relationship between national spending and health outcomes is important to inform policy and health care budgets, not least through the specification of a cost-effectiveness threshold. Karl Claxton and colleagues released a big study looking at all the programmes of care in the NHS in 2015 purporting to estimate exactly this. I wrote at the time that: (i) these estimates are only truly an opportunity cost if the health service is allocatively efficient, which it isn’t; and (ii) their statistical identification method, in which they used a range of socio-economic variables as instruments for expenditure, was flawed as the instruments were neither strong determinants of expenditure nor (conditionally) independent of population health. I also noted that their tests would be unlikely to be any good to detect this problem. In response to the first, Tony O’Hagan commented to say that that they did not assume NHS efficiency, nor even that it was assumed that the NHS is trying to maximise health. This may well have been the case, but I would still, perhaps pedantically, argue then that this is therefore not an opportunity cost. For the question of instrumental variables, an alternative method was proposed by Martyn Andrews and co-authors, using information that feeds into the budget allocation formula as instruments for expenditure. In this new article, Claxton, Lomas, and Martin adopt Andrews’s approach and apply it across four key programs of care in the NHS to try to derive cost-per-QALY thresholds. First off, many of my original criticisms I would also apply to this paper, to which I’d also add one: (Statistical significance being used inappropriately complaint alert!!!) The authors use what seems to be some form of stepwise regression by including and excluding regressors on the basis of statistical significance – this is a big no-no and just introduces large biases (see this article for a list of reasons why). Beyond that, the instruments issue – I think – is still a problem, as it’s hard to justify, for example, an input price index (which translates to larger budgets) as an instrument here. It is certainly correlated with higher expenditure – inputs are more expensive in higher price areas after all – but this instrument won’t be correlated with greater inputs for this same reason. Thus, it’s the ‘wrong kind’ of correlation for this study. Needless to say, perhaps I am letting the perfect be the enemy of the good. Is this evidence strong enough to warrant a change in a cost-effectiveness threshold? My inclination would be that it is not, but that is not to deny it’s relevance to the debate.

Risk thresholds for alcohol consumption: combined analysis of individual-participant data for 599 912 current drinkers in 83 prospective studies. The Lancet Published 14th April 2018

“Moderate drinkers live longer” is the adage of the casual drinker as if to justify a hedonistic pursuit as purely pragmatic. But where does this idea come from? Studies that have compared risk of cardiovascular disease to level of alcohol consumption have shown that disease risk is lower in those that drink moderately compared to those that don’t drink. But correlation does not imply causation – non-drinkers might differ from those that drink. They may be abstinent after experiencing health issues related to alcohol, or be otherwise advised to not drink to protect their health. If we truly believed moderate alcohol consumption was better for your health than no alcohol consumption we’d advise people who don’t drink to drink. Moreover, if this relationship were true then there would be an ‘optimal’ level of consumption where any protective effect were maximised before being outweighed by the adverse effects. This new study pools data from three large consortia each containing data from multiple studies or centres on individual alcohol consumption, cardiovascular disease (CVD), and all-cause mortality to look at these outcomes among drinkers, excluding non-drinkers for the aforementioned reasons. Reading the methods section, it’s not wholly clear, if replicability were the standard, what was done. I believe that for each different database a hazard ratio or odds ratio for the risk of CVD or mortality for eight groups of alcohol consumption was estimated, these ratios were then subsequently pooled in a random-effects meta-analysis. However, it’s not clear to me why you would need to do this in two steps when you could just estimate a hierarchical model that achieves the same thing while also propagating any uncertainty through all the levels. Anyway, a polynomial was then fitted through the pooled ratios – again, why not just do this in the main stage and estimate some kind of hierarchical semi-parametric model instead of a three-stage model to get the curve of interest? I don’t know. The key finding is that risk generally increases above around 100g/week alcohol (around 5-6 UK glasses of wine per week), below which it is fairly flat (although whether it is different to non-drinkers we don’t know). However, the picture the article paints is complicated, risk of stroke and heart failure go up with increased alcohol consumption, but myocardial infarction goes down. This would suggest some kind of competing risk: the mechanism by which alcohol works increases your overall risk of CVD and your proportional risk of non-myocardial infarction CVD given CVD.

Family ruptures, stress, and the mental health of the next generation [comment] [reply]. American Economic Review [RePEc] Published April 2018

I’m not sure I will write out the full blurb again about studies of in utero exposure to difficult or stressful conditions and later life outcomes. There are a lot of them and they continue to make the top journals. Admittedly, I continue to cover them in these round-ups – so much so that we could write a literature review on the topic on the basis of the content of this blog. Needless to say, exposure in the womb to stressors likely increases the risk of low birth weight birth, neonatal and childhood disease, poor educational outcomes, and worse labour market outcomes. So what does this new study (and the comments) contribute? Firstly, it uses a new type of stressor – maternal stress caused by a death in the family and apparently this has a dose-response as stronger ties to the deceased are more stressful, and secondly, it looks at mental health outcomes of the child, which are less common in these sorts of studies. The identification strategy compares the effect of the death on infants who are in the womb to those infants who experience it shortly after birth. Herein lies the interesting discussion raised in the above linked comment and reply papers: in this paper the sample contains all births up to one year post birth and to be in the ‘treatment’ group the death had to have occurred between conception and the expected date of birth, so those babies born preterm were less likely to end up in the control group than those born after the expected date. This spurious correlation could potentially lead to bias. In the authors’ reply, they re-estimate their models by redefining the control group on the basis of expected date of birth rather than actual. They find that their estimates for the effect of their stressor on physical outcomes, like low birth weight, are much smaller in magnitude, and I’m not sure they’re clinically significant. For mental health outcomes, again the estimates are qualitatively small in magnitude, but remain similar to the original paper but this choice phrase pops up (Statistical significance being used inappropriately complaint alert!!!): “We cannot reject the null hypothesis that the mental health coefficients presented in panel C of Table 3 are statistically the same as the corresponding coefficients in our original paper.” Statistically the same! I can see they’re different! Anyway, given all the other evidence on the topic I don’t need to explain the results in detail – the methods discussion is far more interesting.

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