Martin Modrák writes:
Anders Huitfeldt et al. recently published a cool preprint that follows up on some quite old work and discusses when we should report/focus on ratio of odds for a death/event and when we should focus on ratios of survival/non-event odds.
The preprint is accompanied by a site providing a short description of the main ideas:
The key bit:
When an intervention reduces the risk of an outcome, the effect should be summarized using the standard risk ratio (which “counts the dead”, i.e. considers the relative probability of the outcome event), whereas when the intervention increases risk, the effect should instead be summarized using the survival ratio (which “counts the living”, i.e. considers the relative probability of the complement of the outcome event).
I took a look and was confused. I was not understanding the article so I went to the example on pages 15-16, and I don’t get that either. They’re saying there was an estimate of relative risk of 3.2, and they’re saying the relative risk for this patient should be 1.00027. Those numbers are so different! Does this really make sense. I get that the 3.2 is a multiplicative model and the 1.00027 is from an additive model, but they’re still so different.
There’s also the theoretical concern that you won’t always know ahead of time (or even after you see the data) if the treatment increases or decreases risk, and it seems strange to have these three different models floating around.
In response to my questions, Martin elaborated:
A motivating use case is in transferring effect estimates from a study to new patients/population: A study finds that a drug (while overall beneficial) has some adverse effects – let’s say that it in the control group 1% patients had thrombotic event (blood clot) and in the treatment group it was 2%. Now we are considering to give the drug to a patient we believe has already elevated baseline risk of thrombosis – say 5%. What is their risk of thrombosis if they take the drug? Here, the choice of effect summary will matter:
1) The risk ratio for thrombosis from the study is 2, so we could conclude that our patient will have 10% risk.
2) The risk ratio for _not_ having a thrombosis is 0.98/0.99 = 0.989899, so we could conclude that our patient will have 95% * 0.989899 ~= 94% risk of _not_ having a thrombosis and thus 6% risk of thrombosis.
3) The odds ratio for thrombosis is ~2.02, the baseline odds of our patient is ~0.053, so the predicted odds is ~0.106 and the predicted risk for thrombosis is 9.6%.
So at least cases 1) and 2) could lead to quite different clinical recommendations.
The question is: which effect summaries (or covariate-dependent effect summaries) are most likely to be stable across populations and thus allow us to easily apply the results to a new patient. The preprint
“Shall we count the living or the dead?” by Huitfeldt et al. argues that under assumptions that plausibly at least approximately hold in many cases where we study adverse effects the risk ratio of _not_ having the outcome (i.e. “counting the living”) requires few covariates to be stable. A similar line of argument then implies that at least in some scenarios where we study direct beneficial effects of a drug, the risk ratio of the outcome (i.e. “counting the dead”) is likely to be approximately stable with few covariates. The odds ratio is then stable only when we in fact condition on all covariates that cause the outcome – in this case all other effect summaries are also stable.The authors frame the logic in terms of a fully deterministic model where we enumerate the proportion of patients having underlying conditions that either 100% cause the effect regardless of treatment, or 100% cause the effect only in presence/absence of treatment, so the risk is fully determined by the prevalence of various types of conditions in the population.
The assumptions when risk ratio of _not_ having an outcome (“counting the living”) is stable are:
1) There are no (or very rare) conditions that cause the outcome _only_ in the absence of the treatment (in our example: the drug has no mechanism which could prevent blood clots in people already susceptible to blood clots).
2) The presence of conditions that cause the outcome irrespective of treatment is independent of presence of conditions that cause the outcome only in the presence of treatment (in our example: if a specific genetic mutation interacts with the drug to cause blood clots, the presence of the mutation is independent of unhealthy lifestyle that could cause blood clots on its own). If I understand this correctly, this can only approximately hold if the outcome is rare – if a population that has high prevalence of independent causes, it has to have less treatment-dependent causes simply because the chance of the outcome cannot be more than 100%.
3) We have good predictors for all of the conditions that cause the outcome only when combined with treatments AND that differ between study population and target population and include those predictors in our model (in our example: variables that reflect blood coagulation are likely to need to be included as the drug may push high coagulation “over the edge” and coagulation is likely to differ between populations, OTOH if a specific genetic mutation interacts with the drug, we need to include it only if the genetic background of the target population differs from the study population)
The benefit then is that if we make those assumptions, we can avoid modeling a large chunk of the causal structure of the problem – if we can model the causal structure fully, it doesn’t really matter how we summarise the effects.
The assumptions are quite strong, but the authors IMHO reasonably claim, that they may approximately hold for real use cases (and can be at least sometimes empirically tested). One case they give is vaccination:
The Pfizer Covid vaccine has been reported to be associated with risk ratio of 3.2 for Myocarditis (a quite serious problem). So for a patient with 1% baseline risk of Myocarditis (this would be quite high), if risk ratio was stable, we could conclude that the patient would have 3.2% risk after vaccination. However, the risk ratio for not having Myocarditis is 0.999973 and assuming this is stable, it results in predicting a 1.0027% risk after vaccination. The argument is that the latter is more plausible as the assumptions for stability of risk ratio of not having the event could approximately hold.
Another intuition to thinking about this is that the reasons a person may be prone to Myocarditis (e.g. history of HIV) aren’t really made worse by vaccination – the vaccination only causes Myocarditis due to very rare underlying conditions that mostly don’t manifest otherwise, so people already at risk are not affected more than people at low baseline risk.
Complementarily, risk ratio of the outcome (counting the dead) is stable when:
1) There are no (or very rare) conditions that cause the outcome only in the presence of the treatment (i.e. the treatment does not directly harm anybody w.r.t the outcome).
2) The presence of conditions that _prevent_ the outcome regardless of treatment is indepedent of presence of conditions that prevent the outcome only in the presence of treatment.
3) We have good predictors for all of the conditions that prevent the outcome only when combined with the treatment AND that differ between study population and target population and include those predictors in our model.
This could plausibly be the case for drugs where we have a good idea how they prevent the specific outcome (say an antibiotic, that prevents infection unless the pathogen has resistance). Notably those assumptions are unlikely to hold for outcomes like “all-cause mortality”, so the title of the preprint might be a bit of a misnomer.
The preprint doesn’t really consider uncertainty, but in my reading, the reasoning should apply almost identically under uncertainty.
There’s also an interesting historical outlook as the idea can be traced back to a 1958 paper by Mindel C. Sheps which was ignored, but similar reasoning was then rediscovered on a bunch of occasions. For rare outcome the logic also maps to focusing on “relative benefits and absolute harms” as is often considered good practice in medicine.
One thing I also find interesting here is the connection between data summaries and modeling. In some abstract sense, the way you decide to summarize your data is a separate question from how you will model the data and underlying phenomenon of interest. But in practice they go together: different data summaries suggest different sorts of models.
I will be honest and say that I am not sure I get it as well. Deaths are a very rare event and changes in the relative number matter a lot. But if you want to start talking about the absolute risk in the whole population, I am not sure why absolute rates don’t contain more information. I have a lot of issues with number needed to treat or number needed to harm, but that’s the intuition about reporting those parameters to give an intuitive sense of the real risks. It’s trivial to show that they won’t generalize between populations but hazard ratios should if the proportional hazard assumption is true (spoiler: it probably isn’t in any real data).
But reporting risks and harms on different scales seems to make it more difficult to judge the balance between the two, for the people actually using the treatment (the patients). Maybe that is ok for really rare side effects that we want to be discounted (rhabdomyolysis for statins) but there are a lot of cases where the harms and benefits are very close.
When reporting the risks and harms to the patient, I would not rely on any effect measure, and would instead suggest giving them absolute probabilities (i.e. the risk under treatment and the risk under the control condition). The question is really more about which model we rely upon to generate these predictions.
Empirical studies in medicine (such as RCTs) simply cannot report individualized absolute probabilities for every kind of patient (or for every covariate pattern). No study would be powered for this. Therefore, in the work flow that has been almost universally adopted by real-life clinicians, they assume they have the ability to predict risk under the control condition, using information from *outside* the study (perhaps based on natural history of the disease, or prediction models from data collected before treatment was available), and that this can be combined with the “effect size” from a study, in order to predict risk under treatment. This will result in different predictions depending on the scale that is used to report the effect size.
The question about whether it is difficult to interpret the scale really has to take a backseat relative to the much more important question about whether it will lead to good predictions. If you want to simplify interpretation, then just give the patients the individualized predictions (in terms of probabilities) rather than bore them with the mathematical details about which mathematical model was used to generate them.
No. If there are multiple ways to report an effect of a medical intervention, and each effect size leads to a different interpretation, and which interpretation leads to the best application of the intervention depends on context, you do not omit all reportable effect sizes but the one with the most stability over the most cases. You report every effect size, and you report stability over cases. In the vaccine example, you can simply say exactly what Martin said:
“The Pfizer Covid vaccine has [a] risk ratio of 3.2 for Myocarditis…. [F]or a patient with 1% baseline risk of Myocarditis…*if risk ratio was stable* we could conclude that the patient would have 3.2% risk after vaccination. However, the risk ratio for not having Myocarditis is 0.999973 and *assuming this is stable*, it results in…a 1.0027% risk after vaccination.”
The author is free to then talk about plausible arguments given assumptions, but it took literally 3 sentences to fully report results in a way that gives a medical expert all information necessary to draw subtle, context-dependent conclusions about for whom the intervention should be recommended and under what circumstances.
Medicine is not social science: we do not simplify presentation of results to make it more intuitive or less misleading. Or, if we do, we do so in parallel with complicating the presentation of results so that all the information is there for an expert to draw a fully-informed conclusion. Medical experts, unlike social scientists, are only qualified as such if they can grasp subtlety and complexity. If I’m naive and that’s not actually the standard, then a) we have bigger problems than effect size reporting, and the solution isn’t depriving true experts of full information; and b) were I an ambulance chaser, I’d set up an auto-alert on PubMed for articles citing Huitfeldt and look for clients with the complications not emphasized in the articles.
Obviously, it’s different if you’re a medical expert communicating with policymakers or patients, but it’s not my impression that is the context here.
I don’t have the patience to wade through this paper, but I’m stuck at:
“They’re saying there was an estimate of relative risk of 3.2, and they’re saying the relative risk for this patient should be 1.00027. Those numbers are so different! Does this really make sense. I get that the 3.2 is a multiplicative model and the 1.00027 is from an additive model, but they’re still so different.”
Can someone explain simply how these two numbers are derived/compatible? I don’t see how a person with 1% baseline risk is equivalent to the relative risk of 1.00027 in the survival mode.
If you are one of the 1% of people already predisposed to Myocarditis, your risk after getting vaccinated would be 3.2%, or a 1% chance of (getting Myocarditis regardless of the shot) and a 2.2% chance of (getting Myocarditis because of the shot).
If you are a random person from a population where 1% of people have this predisposition, then you have a 1.00027% chance of both (having the predisposition) and (getting Myocarditis because of the shot).
So, what is the relevance of this example? In one case, we are looking at a person with known predisposition to Myocarditis and assessing the risks of getting vaccinated. In the second case, we are looking at a random person from the population and assessing their relative risk of getting Myocarditis after vaccination and being predisposed to the disease to begin with. Why is this case an example of anything relevant? It would seem that different risk assessments should be used if we have a patient who we know is predisposed to Myocarditis and one who is not? Yes, the numbers are quite different, but shouldn’t they be?
Ok, I’ll quite here and leave it to those of you that want to debate the subtle points (this is too much like reading current economics articles). I think the examples are quite misleading as they compare evaluating risks to a person with known risks to evaluating risks to a random person in the general population. Of course, the risk ratio derived applies to a specific population in the study and applying this risk ratio to a subpopulation or a different population can give misleading advice. And of course absolute risk and relative risk are two different things and can convey different messages. But I think this issue of whether the risk ratio is “stable” sweeps a great deal of the issue under the rug. I don’t think that is an innocent assumption. Nor do I think the examples where we pretend to know a person’s individual risk are particularly helpful – in most cases, I believe clinicians have a fairly fuzzy idea of a patient’s individual risk, perhaps only that it may be higher than average or lower than average. So, the precision in these examples seems misleading to me.
Too much detail in the paper for me, just like many economics publications. I’ll read others responses to get an idea whether this work contributes anything to the literature on how best to convey risk estimates (a subject I am interested in).
Michael –
I couldn’t quite follow the post, and please excuse my ignorance – but I have a basic question I’ve been wondering about, haven’t seen it addressed, and maybe you can answer.
> If you are one of the 1% of people already predisposed to Myocarditis, your risk after getting vaccinated would be 3.2%, or a 1% chance of (getting Myocarditis regardless of the shot) and a 2.2% chance of (getting Myocarditis because of the shot).
What is the benefit of that information if you haven’t factored in the risk of myocarditis from infection, and whether risk of myocarditis from vaccination mitigates, exacerbates, or just sits in top of that background risk?
For some additional context, Huitfeldt discusses his approach in this long (and sometimes contentious) thread at Frank Harrell’s DataMethods forum: https://discourse.datamethods.org/t/should-one-derive-risk-difference-from-the-odds-ratio/4403
long and contentious is right. I didn’t know this was still going. I think I stopped reading at comment 200 something and forgot about it.
It’s mostly died down now from the looks of it, but in its prime it was quite the thread. There were three or four separate arguments going on at one point. An RD vs RR vs OR vs switch RR battle royale!
Two legitimate ways of looking at the data should give compatible results. If they don’t, there should be some compelling reason to select one way over the other. Without such a reason, the numbers have no value in terms of motivating some course of action.
People want to know:
1) What percent of vaccinated get myocarditis?
2) What percent of non-vaccinated get myocarditis?
Then if there are identifiable subgroups (eg, age), we want to know that too.
Same for something like smoking:
1) What percent of smokers get lung cancer?
2) What percent of non-smokers get lung cancer?
We do not want to know “the relative risk of a smoker not getting lung cancer.” I don’t see why stats so often seems to involve taking the inverse or complement of what we want to know.
> People want to know:
>> 1) What percent of vaccinated get myocarditis?
>>> 2) What percent of non-vaccinated get myocarditis?
Seems to me like a rather useless comparison.
As opposed to:
Does vaccination increase risk of myocarditis, with considering that (1) infection increases risk of myocarditis, (2) vaccination increases risk of myocarditis, (3) vaccination reduces risk of infection to some extent and, (4) vaccination reduces (some) negative outcomes from infection to some extent.
More specifically, I’d like to know how the risk from infection and risk from vaccination interact. IOW, is the risk from infection and risk from vaccination straight up additive?
And then I’d want to how factors like age, sex, comorbidities, etc. interact with the various risk profiles.
No one actually wants to know this. There is no reason to care about a difference like 0.15% vs. 0.16%, and the answer is going to be “under some circumstances but not others.”
The real question is “how big is the risk, and when do we need to look out for it?” The percentages people want can be used to answer these questions.
There is nothing for me to do with values like “age-adjusted relative risk of *not* getting myocarditis”, it only seems to generate endless paragraphs of discussion riddled with logical fallacies. Angles dancing on pins, if you will.
I think it is very bad form to publicly accuse us of “logical fallacies”, without providing a concrete example of an instance where we committed one. This is an allegation that I take very seriously. I assure you, if you find a logical fallacy, we will correct it, or withdraw the preprint if it cannot be corrected.
Anders:
No kidding! Let me tell you a story about that. Years ago I was up for a promotion review, and they got outside letters. One of the letters was super negative, and one thing the letter writer wrote was that my book (Bayesian Data Analysis, which at that time was in its first edition) had errors. But he did not list any errors in his letter. Not any at all! So I asked the department chair to get back to the letter writer and ask for details. Like you, I take errors very seriously. I followed up with the department chair and he informed me that the letter writer refused to share any details. Presumably because he hadn’t actually found any errors. What a dick. I had no problem with someone pointing out errors, but lots of problems with someone using nonexistent errors to criticize me. I guess the larger goal of playing academic politics was more important to him than the picky, picky business of telling the truth.
In this case, I assume Anon will respond with clarification regarding the logical fallacies and we can go from there.
I didn’t mean to, that was directed at the question “Does vaccination increase risk of myocarditis?”
But in your paper I do indeed find a number of fallacies when attempting to apply your methods to real data:
1) There is no single “effectiveness” of a vaccine. It depends on age, waning, mutations, comorbidity, etc. You do mention mutations, which were expected due to mass vaccination against only the fastest mutating part of the virus. The population included in the RCT was not representative of the population being mass vaccinated, and we do not expect the value to be stable over time.
2) The study did not measure “preventing the original strain of Covid-19”. It measured positive PCR tests within a certain time window, both after vaccination, and after a certain set of symptoms were reported.
3) The first two are simply false premises, the logical fallacy occurs when the 95% number is attributed solely to the vaccine rather than also testing. There was no exit poll performed, but many people report very distinct side effects after vaccination. So it is very likely a large proportion knew whether they were vaccinated or not, which influenced the decision when/if to be tested.
Ie, just because 95% fewer cases reported in the vaccinated group, it does not follow that the vaccine was preventing infection. Or even the more accurate claim of “preventing a positive PCR test within 5 days of a certain set of symptoms being reported from at least two weeks after the second dose up to three months later… in the study population.”
The same goes for myocarditis. People may be more likely to get tested for it because they were vaccinated, especially once it has been in the news. Or perhaps once vaccinated, they are more likely to engage in activities that increase the risk of myocarditis diagnosis (especially if they were following health guidelines and largely staying home for months-to-years prior).
We can’t jump to conclusions just because there is a difference between two groups. Specifically, it is a form of affirming the consequent.
The way to deal with this is compare the relative fit of the various explanations (and possibly combinations of them), using Bayes rule.
> Does vaccination increase risk of myocarditis
>> No one actually wants to know this. There is no reason to care about a difference like 0.15% vs. 0.16%, and the answer is going to be “under some circumstances but not others.”
Talk about fallacies!
You’re assuming that the difference is small, which you can only determine if you’re looking to see if the risk is increased (or decreased)!
> The real question is “how big is the risk, and when do we need to look out for it?”
Another fallacy. There is no one “real” question. Once again you inflate the importance of your personal opinion to equate to some greater reality.
I forgot to add in my earlier comment, the relevance of comparing severity associated with vaccine-induced versus infection-induced myocarditis.
And as I’m sure you know, all of this takes on a magnified importance because of the anti-vax rhetoric about vaccine-induced myocarditis.
I agree 100% that what people want to know, is what percent of people would get myocarditis if vaccinated, and what percent would get myocarditis if not vaccinated. (I.e. exactly what you said, except restated to reflect counterfactual/causal risks)/
The problem is that we may arrive at different answers to that question, depending on how we resolve the theoretical issues that we discuss in the preprint. I assure you, it is all for the purpose of providing valid answers to the things you say people want to know.
I avoided the counterfactual, because that requires additional assumptions beyond the data. Eg, as mentioned above you need to assume the actual injection is the only thing different between vaccinated vs not and pre- vs post-vaccination.
For me to trust a counterfactual there needs to be a model with a reliable track record. Eg, most people would trust solar system astronomers to accurately predict the orbit of an asteroid if there was attempt to alter it (with some uncertainty due to not knowing exact density, etc).
Here is another possiblity: The increased risk of myocarditis only shows up in the ~ 1/10,000 people who had the vaccine accidently injected into a vein rather than the muscle. We have recently learned from evidence-based medicine there is “no evidence” that aspiration during the injection (to check if a vein is hit) has a benefit. Then hundreds of millions of people were given IM injections by inexperienced providers who were not trained to aspirate.
Inject the vaccine into the tail veins of some rats to see what happens.
Thanks for sharing, I found Martin’s response to be quite interesting. These sorts of questions were on my mind a lot when the Myocarditis risk of the mRNA vaccines was a topic of discussion. There was a lot of focus on the probability of getting Myocarditis conditional on having COVID being higher than the probability of getting Myocarditis conditional on taking the vaccine (perhaps this isn’t the most accurate statement but you know what I mean), but very little discussion of whether the people who would get Myocarditis from COVID are the same people who would get Myocarditis from the vaccine. To me these types of concerns are related to the heterogeneity in treatment effects post from a few days ago. It also gets you thinking about why exactly the vaccines had less than 100% effectiveness (e.g. is most of the variation coming from the doses, the people, the subsequent interactions with the virus, etc.)
You would need to add the two. It isn’t getting the vaccine or getting covid, it is covid vs covid + vaccine.
However, the vaccine should protect against viremia. So the course of infection should be different (for some time) after vaccination.
Thank you so much for writing about our work, Andrew. Also, thanks to Martin for the excellent summary!
If I can make a minor comment related to your point about multiple different models floating around, I would add that it is possible to specify a single model that adheres to these principles, by using an unorthodox non-GLM link function that automatically selects between the risk ratio and the survival ratio. The first paper I am aware of to suggest such a model is “Estimation of treatment effects in randomized trials with non-compliance and a dichotomous outcome.” (van der Laan et al, JRSS-B 2007). Independently, Rose Baker and Dan Jackson suggested such a model in arXiv preprint (https://arxiv.org/abs/1806.03471)
In the near future, Daniel Farewell, Rhian Daniel, Mats Stensrud and I will release a preprint which introduces a new, flexible class of regression models called “Regression by Composition”. This work was originally motivated by the need to adhere to these principles while relying on a single model that can be specified before the analyst sees the data, but the methodological framework that we set up turns out to be useful for much more general purposes. Hopefully, this discussion will be clearly when we show how this approach can be used in the multivariable regression context.
What is the benefit of reporting single number effect summaries of risk (like RD, RR, OR, or switch RR) at all? Why not report the risk function? Why is it that summary measures must be reported, when instead there could be plots?
That’s just a limitation of the examples: the more general insight in the preprint is that under the assumptions listed (which are plausible for some types of adverse events) you’ll need a much simpler model to get good predictions for “risk ratio of not getting the event” for new populations than to get similarly good predictions for “risk ratio of the event” or odds ratio. Or, alternatively for a given complexity of the model, you’d get better predictions with “risk ratio of not event”…
Single number is just an extreme case that makes the examples easier to digest.
Ok, but say you run a logistic regression model for some binary outcome. Why not report plots of the predicted probabilities across a variety of levels of the predictors, rather than a ratio of any kind?
Participants in randomized trials are usually not representative of the patients that are seen in clinical practice (being selected, among other things, for not having complicated comorbidities, and for having high risk in order to maximize power in a fixed sample size).
They may differ in terms of covariates that are not included in the logistic model, meaning that the logistic model will not generalize, and will produce non-applicable risk estimates
They could also differ in terms of covariates that are included in the model. If this happens, we are using the model to extrapolate into a region where we have no data. If a logistic model is used, that extrapolation will rely on an assumption that the odds ratio is stable. If instead we relied on model that assumes that the switch relative risk is stable, we might get very different predictions (in particular when extrapolating). In my view, this makes it important to have thought clearly through which of the models we are going to rely on, and why.
It is also worth noting that randomized trials are usually small, and not intended to be powered for risk prediction. Most clinicians would prefer to predict their patient’s risk (under the control prediction) using something other than the randomized trial, and rely on trials only for estimating the effect size. For example, there may exist a huge cohort study that was conducted before the drug was available (enabling us to predict baseline risk without need for randomization), and this may provide excellent patient-specific risk predictions, with much smaller standard errors than the relatively small trial
Doctors may even want to predict baseline risk using covariates that are known to them, but which were not included in the logistic model from the trial. For example, suppose you know your patient has a specific complicating factor that places him at higher risk than other patients, but this complicating factor was not controlled for in the model. In such settings, it is desirable to separate the procedure that predicts baseline risk, from the procedure used to predict effect size.
Thanks for the thorough explanation! Your last two paragraphs make sense to me. Honestly, that sounds like a tough task to do, as everything seems conditional to me, so it seems like any regression model would be inadequate in this scenario, but I guess your argument is that there are some worse than others.
>They may differ in terms of covariates that are not included in the logistic model, meaning that the logistic model will not generalize
>They could also differ in terms of covariates that are included in the model. If this happens, we are using the model to extrapolate into a region where we have no data.
This would seem to apply to any regression model in any scenario…
>If a logistic model is used, that extrapolation will rely on an assumption that the odds ratio is stable. If instead we relied on model that assumes that the switch relative risk is stable, we might get very different predictions (in particular when extrapolating).
Perhaps a dumb question, but could you not compute the switch relative risk from a Bayesian bernoulli model with logit link (logistic model) by making predictions of probabilities and using the posterior samples to compute? I see your argument against the OR as an effect summary, but does this have to apply to the logistic model?
Yes, exactly, This is a very difficult task and any regression model will be “wrong”, but some models are less wrong than others. Since we don’t really have any good alternatives to regression models, we have to choose the least bad option. If we are going to extrapolate, we should extrapolate based on the model that best matches our biological beliefs. One thing that makes the switch relative risk model less bad, is that we can use application-specific biological knowledge to reason about whether we think the model is plausible in our specific setting.
As you say, you could in principle use a logistic regression model to make predictions, and then convert to switch relative risk. I would not do so in practice. Let’s consider a highly stylised example:
Suppose we have a randomized trial run in Norway, and that we analyze the data with a regression model, controlling for sex. We now want to extrapolate the results to the United States. We have two choices to make, which are in principle distinct: Which link function to use in the regression model, and which effect measure to use extrapolate from Norway to the US.
If we choose a logistic model to analyze the data, it means that we are imposing a homogeneity assumption that says that the odds ratio in men in Norway is equal to the odds ratio in women in Norway. In contrast, a switch relative risk regression model would make a similar assumption on the switch relative risk scale.
We then extrapolate the results either marginally (by predicting the marginal odds ratio in the trial), or conditional on sex (by predicting both conditional odds ratios). If we choose the first approach, we are making the assumption that the marginal odds ratio (or marginal SRR) in the US is equal to the corresponding effect measure in Norway. If we use the second approach, we are assuming that the conditional odds ratio among American women is equal to the conditional odds ratio among Norwegian women, and similarly for men.
In other words, both the question about which link function to use, and the question about what quantity to extrapolate, are at their hearts about homogeneity assumptions between groups. The groups that needs stability differ, but the same kind of logic applies in both cases. It is in principle possible to have different beliefs about the most suitable scale for each between-group comparison, but in both cases, only the switch relative risk has a biological rationale.
Stated differently: In my view, a regression model is best understood as a homogeneity assumption, where the scale of the homogeneity assumption is determined by the link function. The logistic model is exactly equal to the set of joint distributions that are consistent with effect homogeneity on the odds ratio scale, between groups defined by the covariates in the model. If such homogeneity does not hold, the model is misspecified, as the true joint distribution will not be contained in the model. We can reason about such homogeneity using the same principles as we use to reason about homogeneity between countries, though our conclusions could in principle differ.