Probably because:

1. All predictive models are not least squares regression

2. In prediction validation is more important.

Best wishes, David Booth

Tiago Rodrigues Tavares , both your statements are wrong. From what source is this information?

Tiago Rodrigues Tavares Perhaps people are less concerned about violations of these two assumptions of OLS regression (normality and homoscedasticity of errors) because violations of these assumptions mostly affect the standard errors (i.e., statistical inference, tests of statistical significance), whereas the parameter estimates themselves are not strongly affected.

Jochen Wilhelm, thanks for your criticism, I think I expressed myself better in the text now. In fact, I am referring only to linear models that use OLS for parameter estimation (e.g., simple and multiple regressions and PLSR). As far as I know, these models need to have residuals with normal distribution and homogeneity of variance; however, I don't see in papers in my area the presentation of Shapiro-Francia and Breusch-Pagan tests, for example. Usually, what is done is the evaluation of performance indicators (e.g., RMSE, RPIQ, RPD) in a validation using an independent sample set.

The OLS is a short cut to the ML solution. It can be derived directly from the assumption that Y|X ~ N(µ(X), s²), but the solution is correct for any distribution model: justlike the ML estimate, the OLS estimate estimates the expected value (of the parameter) and this is independent of the assumed distribution model ("under some mild regularity conditions", eg. as long as it has a finite expectation and variance).

The difference, therefore, is not in the predicted value, but rather in the uncertainty attributed to this prediction. Depending on the research context, this uncertainty may or may not be relevant. If it is not relevant, then there is no need invest much mental work in figuring out a "most correct" or "least wrong" distribution model.

When models are really used for prediction, the "model inherent" uncertainty (that is determined by the chosen distribution model) associated with a prediction is usually not relevant. What is of much greater relevance and impact here is the differences in predictions between possible alternative models. This is particularily relevant when the predictions are forecasts. Provided there is sufficient data, this pleiotropy of possible alternative models can be adressed by heavily over-parametrized models where the impact of the assumed distributional model approaches zero (such models are nowadays called "deep-learning" models, neural networks, AI etc,). This is then very much on the side of getting most correct predictions at the cost of gaining the least amount of insight. But it works to get predictions with good or acceptable positive and negative predictive values.

Checking model assumptions is about scientific integrity. When questioned, the response I often get is something equivalent to "how dare you assume that I don't" or "everyone does that." When I can check independently, some do and others not so much. Tests of model assumptions are not published because the outcome has no bearing on the primary research topic (assuming that the analyses were done properly). Trust me is easier and faster than proving it every time.

The other part of this is good scholarship. In reading a paper on their favorite (non-statistics) topic do most people miss a 3 to 5 page discussion on model validity? I do not even remember the last time I saw a discussion on how the data were cleaned or what mistakes were corrected. If the data are not clean, the analysis is unreliable and model assumptions unimportant.

I never see these issues published, so I don't require them when I am a reviewer (and realize that perpetuates the system). On the other hand, I have tried to include some of this in my manuscripts and coauthors or editors complain that the manuscript is too long, not focused, or just reject it.

I hope that published work is of good quality with appropriate consideration of model assumptions rather than the model assumptions were "overlooked." Of course, there is no way of knowing.

I would point out that statistical tests for model assumptions only "prove" that the assumption was met if a failure to reject the null hypothesis is proof that the null hypothesis is true. This is not consistent with how other statistical tests are interpreted. At best one might argue that a failure to reject is an indication that the departure from model assumption is small enough that the robustness of the method will overcome any problems.

Timothy A Ebert , "Checking model assumptions is about scientific integrity." - this is a very relevant point. I just want to note that this is about understanding, and that prediction serves a different purpose, as deep-learning models demonstrate well these days.

I somewhat disagree with your final note about statistical tests of assumptions. There is so much "hope" involved that one can as well forget about such tests alltogether and formulate one's reasonable hopes right away. It's still ok to have a look if the data strongly contradict these reasonable hopes, but I don't see how testing some hypothesis would be helful here or why a "failure to reject" should indicate some absence of relevant departures, even of those considered relevant.

Tiago Rodrigues Tavares

There is generally too much emphasis put on statistical tests.

Statistical tests are only useful to detect gross (aka extreme) departures from the model. Rather than using statistical test (which can help to a certain extent), plot the residuals, you will be able to detect departures from whatever you are assuming.

Think about it: there are so many tests of normality that you can certainly find one that proves your point - this is not the way to go.

Normality of residuals and homoscedasticity are nice to have (for standard errors) but there are methods that do not require either (resampling, robust standard errors, etc).

Timothy A Ebert if the errors are really coming from a normal and we test that assumption (or any other), the resulting p-values will be uniform over (0,1), and as a result you can easily get small pvalues that most people would compare against the infamous 0.05: statistical tests have way less practical use than it is thought.

Jochen Wilhelm As with other tools, I generally see the tendency to prove that the one model we want to publish is the best, while sometimes there is more than one model supported by the data and it is just as reasonable to compute estimates and predictions from model averaging.

I was curious to know your take on Multi-Model Inference.

Stefano Nembrini , I am not a fan of what is said to be "multi-model inference" that is essentially based on model averaging (be it Bayesian or something else), as I am not a fan of prediction tools that work well but conceal understandable rules of how these predictions are made. I am not saying that such models are not useful. They are surely useful. But prediction for the sake of prediction is just not my cup of tea. I like models as tools to formulate our mental concepts of (certain aspects) the world. The structure of a model can give us new ideas, make us recognize relationships between things we haven't considered so far, help us to recognize more abstract views, provoke "inductive thinking". I think this is just kind of abandoned or lost when averaging different models or using hyper-parametrized or rank-based models. As I said, these are all valuable tools to so something, but this "something" is more on the practical "engeneer-like" side than on the theoretical "scientist-like" side. My interest is more on the latter.*

* Please don't get me wrong: I am not valuing "theory" against "practice" - these are just more or less different domains [with important connections]. They stand side-by-side. It's not that one would be more important, more relevant, or more valuable than the other.