For a specific exposure-outcome combination of interest to you, specify which lifecourse model is likely most appropriate and why you think this is the case. Describe the regression models you could use to test your hypothesis. Are there any possible data sets in which this test could be conducted, and if so, what concerns would you have about interpreting your proposed test of the lifecourse model?
Obesity / BMI and premenopausal breast cancer incidence is not yet well understood. Most studies find that higher BMI in adulthood (prior to menopause) is inversely associated with premenopausal breast cancer risk. However there is some suggestion that obesity / BMI around puberty may play in independent role in affecting breast cancer risk – it is suggested that adiposity around puberty may incur protection for later breast cancer risk irrespective of adult BMI.
There is a large and increasing body of literature suggesting that puberty (menarche) and breast development (thelarche) may be a critical or sensitive window of susceptibility to harmful exposures as the period is marked by large fluctuation of hormone and rapid proliferation of the breast tissue.
Most of the datasets that have data on both adult and adolescent height and weight collect adolescent data retrospectively. There is one study that I know of, the Breakthrough Generations Study in the UK, that has prospective data on adolescents some of whom have now reached adulthood but I don’t think they have enough cancer outcomes to yet look at this question with adequate power. If using retrospective data, you could fit a logistic regression model, including terms for early life BMI and current (adult) BMI and an interaction between the two to see if obesity at both times is worse than one or none – similar to one of the approaches used by Mishra et al. The interaction looks to see if the “social mobility” effect exists – where we would be looking at the effect of early life exposure to obesity and if that effect can be later modified by adult BMI. This is consistent both with the sensitive period approach and the social mobility approach to lifecourse models described by Mishra et al.
There are tons of limitations to this approach – the first being that self-report of height and weight around puberty is likely to be bad. This will likely be non-differential by case status and would attenuate the effect of early life BMI. Another big limitation is that the timing is impossible to decipher – it is hard to define puberty and unlikely that someone’s self-report will correspond completely accurately. We also don’t really know the biological mechanism behind this phenomenon, and the public health message is not clear – if obesity in adolescents is protective for later breast cancer risk, what is the message there? We clearly should no advocate for children to be overweight or obese as these are strong risk factors for other more common conditions both in adolescence and adulthood.
Natalie
Does the British birth cohort have good BMI data? How did the US obesity epidemic affect breast cancer rates for cohorts who hit puberty before vs after the onset of the epidemic?
If you did find evidence that higher BMI at menarche was reduced pre-menopausal breast cancer risk, I suppose the public health message would depend on the mechanism. Seems useful to know though, even if the implication isn't necessarily that 10 year olds should gain weight.
Exposure: Gender reassignment surgery
Outcome: Depressive symptoms
Recently there was a study comparing transgender patients who had gender reassignment surgery (GRS) and age-matched, neighborhood-match controls that showed that those patients who had GRS had an increased risk for all cause mortality, in particular suicide. The authors then claimed that GRS does not fix gender dysphoria and still puts individuals at increased risk for all cause mortality.
I would like to do a lifecourse study of those patients who have undergone GRS at different times in their life. What would make this challenging is that there are large differences in secular trends throughout the lifecourse (i.e. more accepting of transgender individuals as time increases). However, it is not known at which age someone should undergo GRS and whether or not having GRS at earlier ages is beneficial (or not). Whether there is a critical period or an accumulation effect (or both) is not known. Perhaps GRS is more beneficial at different ages. We could use a linear regression model to test our hypothesis. I do not believe there is any current data sets to answer this question. However, we could send out a cross-sectional survey to determine depressive symptoms in our own cohort. We could compare age at time to GRS and depressive symptoms (accumulation of more time after GRS could show an accumulation effect) or compare those who might have been at a critical time point (say 18-25) to those who were outside of this critical time point. I'm now doubting whether or not this is a good example because the exposure can only happen once and thus does not change over time?
Thomas
That's a really interesting example! I think there are two exposures really: exposure to gender dysphoria (which may have cumulative effects with ever accumulating adverse consequences) and GRS, which may (or may not) end the exposure to gender dysphoria but also may have its own set of adverse consequences.
I think your approach of evaluating how people who received GRS at different ages compare w/r/t depression to age-matched individuals who never had gender dysphoria and to themselves prior to GRS makes sense. You could say the effect of gender dysphoria is characterized by comparing trajectories of depressive symptoms among gender dysphoric to non-dysphoric (?) people across age, and the effect of GRS is estimated by comparing the individual pre-post GRS (taking into account time since surgery), but for the individual pre-post comparisons you need to account for the normal effect of age on depressive symptoms (in gender dysphoric or non-dysphoric people), so pre-post GRS compared to changes over the same age range for someone who did not have GRS.
Not easy! And I agree, you are going to have a tough time finding enough data.
One particular question of interest to me is how tobacco smoke exposure at a young age can lead to respiratory conditions in adolescence or early adulthood. I think this would be measurable under the critical period model or the accumulation model. I think it could work under the critical period model because I think that exposure during the first few years of life (including prenatal exposure) could have a long-term impact on respiratory health. However, since secondhand smoke is something that might persist over time and become more frequent later in life, it might also be appropriate to use the accumulation model. For the purposes of this question, I will focus on the critical period model to emphasize how youth exposure to tobacco smoke might affect respiratory development, leading to morbidity.
I would focus specifically on family smoking, and would ask questions about smoking history before and after a child’s birth to better understand intensity of exposure. Current research has shown that in young children (under 2 years of age), secondhand smoke can lead to increased respiratory morbidity. I want to build upon these findings to determine if long-term youth tobacco exposure leads to acute or chronic respiratory conditions in adolescence or early adulthood.
I would measure my outcome, respiratory morbidity, as number of respiratory condition diagnoses over time (acute and chronic). Thus, I would use Poisson regression to measure this association. I could also measure pulmonary function as an outcome using a PFT or some equivalent tool, which I could then use as a continuous outcome variable in a linear regression model. I would also try to account for potential interaction between tobacco smoke exposure and SEP. I think I could get this data from a longitudinal study, such as the Generation R Study, which is a population-based study in the Netherlands following children from pregnancy onwards. I would need not just patient information, but also family information that would answer questions about tobacco exposure.
I think this question does have some major limitations. In particular, there are a myriad of ways an individual can be exposed to tobacco smoke outside of their household. This is not something that can be easily measured and would definitely be hard to completely measure during this critical period. Thus, I would have to interpret my findings as secondhand smoke exposure in the home, as opposed to more generally.
Josh
Smoking is a nice example of an exposure where alternative lifecourse models are appropriate. The key question is whether the critical period model or the accumulation model best describes the link between STS and respiratory conditions. Given that you focus on adolescent outcomes, the typical lifecourse models periods do not apply (e.g., childood, adulthood, late life), so what specific periods of a child's life would you consider? ie the first year? prenatal exposure? The challenge here is that STS exposure is probably highly correlated across the child's life- if dad smokes during the pregnancy, he'll probably smoke in year 1 and year 2 etc. But still it is important to specify a model that allows you to test whether it is specifically STS exposure in infancy that is differentially detrimental to the child's lung development or any STS exposure at any point in childhood.
Although much of the morbidity and mortality from prescription opioids is a result of diversion and illicit use, increases in opioid addiction might be caused by legitimate medical use. The phenomenon known as “iatrogenic addiction” has been thought extraordinarily rare, especially in the context of brief exposures for acute pain. However, evidence suggesting a low risk of iatrogenic addiction is limited in quality and challenged by the skyrocketing rates of opioid addiction that directly parallel similar increases in opioid prescriptions.
I am interested in whether emergency departments (EDs), or the medical system as a whole, might sometimes provide the initial or ongoing exposure to opioids that is ultimately followed by addiction, injection drug use, overdose, or death.We examined this before in convenience sample of patients who presented to the ED with ODs, and many cited previous exposures (http://goo.gl/WJoX0L). Hence, I think this would be fitting for an accumulation/cumulative framework.
The exposure, would be an ongoing prescriptions to narcotics. This is hard to get handle of, as state based narcotic registries are pretty recent. However, an integrated health system like Kaiser Permanente might be suitable, as Prescription, Pharmacy history are linked. We could follow people from birth and measure each occasional insult/hit (a opioid RX).
Exposure: (Multiple) Medical Prescription of Opioids, measured by Prescription Fills for Narcotic class medications. Each fill could characterized in a binary fashion, as well as a continuous fashion (with mg equivalent of morphine) noted.
Outcome: (Iatrogenic) Addiction. Would look at first onset of a diagnosis code of opioid substance abuse.
Limitations:
Identifying the genesis of addiction, and interplay with other comorbidities including mental health disease.
Opioid diversion from other sources, and recreational/non-medical use
Cyrus,
A very timely and important question. Can you specify an alternative hypothesis for how opioid prescriptions influence addiction risk, to compare against the accumulation hypothesis?
Is it plausible that age or timing of first exposure to opioids influences risk of subsequent addiction (e.g., first exposure at age <21 vs older)? Or co-occurring events in the person's life at the time of first exposure increase risk of transition to addiction? Or do you think there's simply a finite chance of addiction w/ each prescription, and they add up?
I agree that Kaiser data would be a good resource, depending on your alternative hypothesis (e.g., if what matters is whether you are unemployed at the time of your first prescription or you are having other sources of personal distress, you can't address that well in Kaiser).
Thanks Maria.
I sense a tension (or conflict of interest?) as a researcher, between:
the life course model, and the countless elements that could be contributing to the genesis of any illness
vs.
the limited data available
Or, put another way, I prefer the simple finite/additive model, because it is something that is available, and measurable (ED visits, RX opioids, etc). Indeed, life does not occur in discrete episodes of ICD9 codes, but my data does. Perhaps this is academic laziness? Or is it being practical. When is a methodology "good" enough?
Classmates, any thoughts?
What is "good enough" depends on what you plan to do with the results. If your goal is simply to show that something at some point in time matters, you don't have to be specific about lifecourse timing. If your goal is to use the evidence to design an intervention, you're going to need to figure out if the timing matters. Many interventions seem like they fail because they are delivered at the wrong time, often based on observational evidence that didn't evaluate the timing with enough specificity..
Exposure: incarceration; outcome: SBP
I think an interesting lifecourse question would be whether incarceration prior to age 18 has a worse effect on trajectory of SBP across life than incarceration after age 18 (or no incarceration). This would be a sensitive period model. I would hypothesize that incarceration prior to age 18 would be especially bad because it would create an interruption in development with lasting effects on health. For example, it would reduce the likelihood of completing high school, which in turn creates greater barriers to employment, etc.
I think you could use the National Longitudinal Survey of Youth to test this hypothesis, because it follows people from their teens into their fifties, and probably includes more detailed questions about incarceration at each time point than any other national longitudinal survey. The model might be a growth curve model similar to that used by Willis et al., which estimated SBP trajectories across the lifecourse. I think you'd incorporate interaction terms as in Mishra et al. to allow slopes to differ depending upon different patterns of incarceration (eg none, before age 18 only, after age 18 only, before and after age 18).
There would probably be lots of problems with this. For one, you'd need enough people who had these different patterns of incarceration to have sufficient power to compare trajectories. In a general population sample, this might be tough. Furthermore, people who did experience incarceration might be more likely to have dropped out of the survey. Secondly, I'd worry about confounding when comparing these different groups. Thirdly, it would be a bit crude in that what I've described here uses binary variables for incarceration, when periods of incarceration might vary dramatically. If length of stay has an effect on SBP, this would be a problem. Related to this, I have grouped people who were incarcerated once after age 18 with people who were incarcerated 50 times after age 18 into a binary variable for adult incarceration.
Alyssa - this is a really interesting question, but if you found out the answer was "yes", earlier incarceration is worse, what would you do with that result? Would it convince people to avoid incarceration of kids?
I think overall people are not moved by evidence on the cardiovascular health effects of incarceration (though maybe some other outcomes might be more compelling- eg future incarceration risk or social outcomes?).
Has anyone ever looked at how your assigned cell mate in prison-stays influences your subsequent outcomes? There's all this literature on peer effects in schools and colleges- basically leveraging randomly assigned college roommates or classroom peers - and maybe it is also relevant in prisons, but is it possible to examine that?
I would be interested in applying the relationship between unhealthy alcohol consumption and premature adult mortality to life course theory.
I think that the relationship between alcohol consumption and the life course remains generally controversial. In almost all countries, legal drinking-age limits exist. In some countries such as the US, these age limits are enforced. Even here, the age limits are often broken, suggesting that some people believe that these age limits are pointless.
In other countries like Uganda, there are age limits for drinking but they are not enforced, resulting in widespread access to alcohol among sometimes very young people (e.g., 10 years old).
Personally, I think that legal drinking age limits emerged mostly out of (conservative-values-based) religious politics. I doubt that there is strong evidence that a 21-year old drinker would be much better off than a 16 year old one. Of course, age limits are, in general, very emotive subjects and this is not restricted to alcohol consumption but to many other things that are considered as "adult behaviors" ranging from sexual activity, through driving, to alcohol consumption, to entry into night clubs. I doubt that any of the associated restrictions are evidence-based. My own views on what should be legal drinking age is perhaps around 15.
I suspect that people who support conservative (i.e., the highest limit possible) age limits do so in the belief that these exposures follow a "critical-periods" model. I.e., if people get exposed to alcohol at a young age, they are more likely to experience negative health outcomes during that time and later. I do not think that this model is true with respect to alcohol and perhaps even the other exposures. And if the accumulation model is the true one, i.e., if you start early you will cumulatively have drank more by 50, and this will kill you early, then it may matter less when you start. You could start at 30 and still drink enough to kill you. Concurrently, your neighbor, who started drinking at 15 might cumulatively gain more self control and be less likely to experience negative outcomes later (my speculation).
I think one way to preliminarily test this question (Does the age at which you start drinking really matter? And what might be the right age to start?) is to do a case control study in one of the countries such as Uganda, where age limits are not enforced. In a case control design, one can possibly test whether those with an important outcome in adulthood, e.g., alcohol dependence, were more likely to start drinking early, and whether the average age at which they started drinking would be different between cases and controls. I do not know any existing database able to answer this question and I would have to primarily collect the data. One regression model would determine the average age at which cases start drinking while controlling for SES, home brewing of alcohol, perhaps sex, and perhaps, parental alcoholism.
Stephen,
A sensitive period model seems plausible to me in this case, but I agree, it's testable. The US changed the legal drinking age from 18 to 21 in the 1980s - that could be a nice natural experiment.
I'd be surprised if nobody ever evaluated it, in particular related to automobile fatalities.
Re cross-national comparisons: why use a case-control design? Could you identify alcohol related deaths from vital stats?
Early childhood growth and long term pulmonary and survival outcomes in cystic fibrosis patients is an area of research in which I have been actively involved. The Cystic Fibrosis Foundation has been making growth and nutritional recommendations for all cystic fibrosis patients since 1992. The most recent nutritional recommendations in 2008 stated a goal of weight for length (WFL) ≥ 50th percentile by age 2 years for all cystic fibrosis patients as well as a goal of BMI ≥ 50th percentile for all children aged 2-21. This recommendation was based on simplistic models built without taking lifecourse into account. There is sufficient data to suggest that early childhood growth may lead to greater lung capacity later in life and perhaps greater reserve, as it is well documented that early linear growth is associated with larger lung volumes. In the international literature looking at stunting, it is clear that if optimal macro and micro nutrient intake is not obtained before age 2, children will remain stunted throughout life despite achievement of adequate nutrition after age 2 years. Furthermore, better nutritional health early in childhood may also enable children to build up greater muscle mass and expectorate the thick secretions of cystic fibrosis without as frequent infections and colonizations with known pathogens like pseudomonas. Additionally, after comparing centers that encouraged robust nutritional interventions versus those that are more timid given the difficulties of getting adequate calories into these patients many studies found aggressive nutritional interventions to be correlated with better pulmonary and survival outcomes.
I think it would be very interesting to examine this issue from both a sensitive period and cumulative effect modeling. The cystic fibrosis foundation has been collecting data on the majority of US subjects cared for at one of the >120 CFF accredited centers across the US since the late 1980s. There is a wide variety of information available in this registry including birth weight, growth parameters, socioeconomic status, what types of formula the patient was taking, methods of diagnosis etc. The data set is broken into annualized data, encounter based data (usually every 3 month visits at a CF center) and episodic data which should be filled out every time a patient is hospitalized. It follow approximately 30,000 subjects annually. We could potentially use a mixed model for FEV-1 percent predicted (a commonly used measure of lung function in this population). In previous models FEV-1 percent predicted is evaluated using linear regression as it is a continuous measure and felt to be normally distributed. I would argue that it is a fairly peaked distribution but probably somewhat normally distributed in each age/sex group. Our main predictor of WFL and or BMI percentile could be conceived as continuous or could be categorized as is often seen on growth curves and utilized by pediatricians. We could define a sensitive time period of birth to 2 years and the later life effect modifiers of BMI percentile from age 2-18 years. Other factors to include in the model might be genotype information (available in the dataset) which may predict more or less severe phenotype, socioeconomic status, cystic fibrosis related diabetes, pancreatic exocrine insufficiency and potentially colonization with certain microbes by certain other ages.
Exposure: Antibiotics exposure
Outcome: Development of Pediatric Ulcerative Colitis
There is ongoing investigation into the impact the microbiome has on the development of inflammatory bowel disease both UC and CD. One of the major ways we impact our micro biome outside of diet and geography is exposure to antibiotics. There has been thought that childhood exposure to antibiotics increases a risk for IBD but most of this work has been done retrospectively often with parent reporting of antibiotic exposure. I am not sure of any database that would make it easy to answer this question prospectively in the US. Having recently attending a conference with a presentation by a Canadian IBD physician/epidemiologist some of the Canadian health datasets might be more able to answer this question as there are some more datasets that can be merged. Ideally, I would have access to a pharmacy database that could capture the antibiotic exposure of all children in one region and then the number the of Pediatric Crohn diagnoses in the same region.I would also need to capture other important pieces of data, such as family history, growth, and ideal to have genetics but likely would be impossible. In an ideal world it would also be great to have related micro biome data, but I don’t know that that is feasible especially in a cohort study, and you would have to get so many samples in order to capture pre and post. It would be interesting to look and see if antibiotic exposure in childhood does increase the risk and if there is a critical window, perhaps exposure after age 2 doesn’t matter, etc.
Melissa,
Could you do this in a comprehensive EHR database that has people longitudinally and all pharma records, e.g., Kaiser, or maybe group health? I guess they would not have anything on genetics or microbiome directly. Family history you might be able to- I don't know if they can link records based on family relationships (even though presumably they have a lot of family members).
Does the UK biobank have any gut microbiome data?
Interesting problem.
Danielle, that's a very cool idea. You could definitely evaluate whether there's some age at which BMI improvements are less (or more) beneficial for subsequent functional outcomes or functional trajectories. Your mixed model can use baseline or past values of BMI and/or time updated values or change in BMI as the relevant exposures.
Exposure: Exposure to trauma
Outcome: PTSD
I would choose the critical period model to measure this relationship (although the accumulation model could also be used). My reasoning is that exposure to traumatic events when critical brain structures are growing and maturing in childhood have lasting effects on the development of future emotional disorders http://www.ncbi.nlm.nih.gov/pubmed/22112927). Logistic or ordinal regression models could be used to predict PTSD-related symptoms among trauma-exposed children and controls. Multilevel analysis could include parental attachment and interactions, sibling peer interactions, etc.
There is only one dataset I know of that has collected these kind of data (http://www.nature.com/tp/journal/v4/n3/pdf/tp20146a.pdf), and I would be concerned about secular trends (i.e. more sensitive to violence as societies become more advanced) and the length of follow up (the population in the data above may future health risks that haven't developed yet.
Great example. It's hard to believe that it follows a strict childhood critical period model, because adults can definitely develop PTSD after trauma exposure, but maybe childhood traumas do have a disproprtionate consequence. Nurses health study II has retrospectively collected data on timing of trauma exposure an PTSD symptoms. They are focused on cardiometabolic consequences of PTSD more than modifiers of the link between trauma and PTSD though.
Exposure: Alcohol use prior to transplant listing
Outcome: Relapse post-transplant
I currently am working on research projects in the field of liver transplantation. Though I can’t think of a question directly related to the problems I’m investigating currently, this is a question that I thought would be well adapted to a life course model. In liver transplant, it is a priority to optimize the use of a limited resource of livers available for transplant. One of the ways to do so is to ensure that recipients whose liver disease is due to alcohol use does not proceed to relapse post-transplant as relapse can have detrimental clinical outcomes. Moreover, if transplanted organs are misappropriated to people that are going to not make the full use of the organ, this could have a deleterious impact on how liver transplant is perceived on a societal level. Thus, I’m interested in what factors are most predictive of relapse to significant alcohol drinking after liver transplantation. Specifically, I’m interested in how the amount that is consumed in different periods (let’s say 0-3 months, 3-6 months, 6-12 months, 1-2 years) preceding the listing of the patient on the waitlist effects the likelihood of relapse post-transplant. I’m not sure if there is a critical period or accumulative effect. I would model this using logistic regression. It has been shown that drinking <6 months before transplant increases risk of relapse, but I think it is important to understand how the different time periods relate to chances of relapse. This could impact transplant policy and how ethics committees decide how to list/transplant patients. I’m not sure if this data exists in the type of granularity that I want on a national level. I work with the UNOS/OPTN database quite a bit, which would house this type of information if it was out there. I think this would have to be done via retrospective chart review at a particular site, but I have a hard time imagining that the level of detail that is desired could be obtained. Perhaps we could look at this problem in terms of general relapse after a certain period of abstinence, which might increase the chance of finding a suitable dataset. Though, it would be a stretch to generalize results from a non-transplant setting to a transplant setting.
James
Thanks for this interesting example. Is this a causal question or a predictive question? It seems like you are really interested in predicting who will relapse post-transplant, not necessarily with the goal of delivering interventions to those people prior to transplant, but rather just to select patients for receiving a very limited resource (a new organ). So, it seems more like a prediction question than a causal question. Given that it's a prediction question, you actually can use everything under the sun to predict as well as possible and you do not need to be precise about the timing. It's still useful to ask "which time period of alcohol use is most predictive" because it might tell you where to invest resources in measuring but from the analysis perspective, just throw it all in there and look at the predicted relapse value. You don't need to test coefficients for one time period against those for another time period and say "0-3 months prior is more important than 4-8 months prior...". You only need to draw that type of conclusion if you want to intervene to prevent drinking prior to transplant and have to choose when to deliver the intervention.
Re the general question of whether these models are relevant to transplant, I was recently involved in a paper that evaluated how wait time for (heart) transplant influenced post-transplant outcomes. I believe their theory was that some of the impact of living with a dying heart accumulated with longer wait times and even once someone got a transplant they still suffered health consequences of the long waiting period. This seems akin to the lifecourse models, with the competing models being the only relevant question is whether you have a healthy heart right now (immediate risk) or it is also relevant that you had an unhealthy heart for some long period of time prior to transplant (accumulation). They were interested in the problem to help evaluate the trade off between taking "lower quality" organs with shorter wait times versus insisting on a higher quality heart even though the patient would have to wait longer for a transplant.