To specify FPCI, we will describe the basic language for encoding causality established by Rubin and called the Rubin causal model (RCM). Since RCMs are partially observed random variables, it is difficult to translate these terms into reality with real data. Therefore, we will use simulations from a simple model to illustrate how these variables are generated. The second virtue of this model is that it will clearly indicate the source of choice in treatment. This will be useful for understanding the biases of intuitive comparisons, but also for discussing causal inference methods. A third virtue of this approach is that it clearly establishes the relationship between the literature on treatment effects and models. Finally, a fourth reason why it is useful is that it will give us a source of sample variation that we will use to visualize and examine the characteristics of our estimators. Now imagine the very long causal diagram with many time points k = 0.1. K, which represents a sequentially randomized trial in which treatment Ak is randomly assigned at each time point k, based on previous treatment and history of the covariate (A ̄k−1,L ̄k). The causal diagram would never contain k direct arrows of unmeasured risk factors U in the Ak treatment. In this sequential randomized trial, treated and untreated subjects are interchangeable at any time k, based on the covariate history prior to L ̄k and the treatment history A ̄k−1.

That is, the sequential interchangeability Yg∐Ak| The ̄k,A ̄k−1 is valid for all times k = 0, 1. K, and we say that there are no unmeasured confounders over time. Under sequential interchangeability, we can obtain consistent estimates of the mean causal effect of a treatment strategy using all anamnesis-adjusted methods (A ̄k−1,L ̄k), such as normalization and IP-weighting. The sequential interchangeability condition Yg∐Ak| The ̄k,A ̄k−1 can be easily weakened. We can use single-world intervention graphs (Richardson & Robins, 2013) to graphically derive these lower sequential interchangeability conditions for static and dynamic regimens. At least 50% of the information needed to calculate ICE is missing, so quantifying ICE may not be a particularly easy task. Classical linear statistical methods are based on the (mostly implicitly) simplistic assumption of the additivity of unit processing, implying that processing has exactly the same effect on each experimental unit. When the hypothesis is abandoned, things get complicated. Neyman (1923) first defined individual causal effects, and he was aware that these could vary from unit to unit.

But he also knew he needed assumptions beyond the data to estimate it. This may have led him to believe that these effects are not interesting or relevant (Neyman 1935, 126): advances in physical world modeling will lead directly to advances in estimating increasingly accurate unit causal effects in the physical world. Various statistical analyses can be used to support causal claims based on observational data. Each technique aims to simulate the conditions of an experiment and does so by introducing certain theoretical assumptions. One approach is to use multivariate analyses to eliminate pre-treatment differences between the treatment and control groups. For example, multivariate regression eliminates covariance between the treatment variable and other observable factors thought to affect the dependent variable. This approach works as long as no unobserved or imperfectly measured factors remain correlated with the treatment and outcome variables. Unfortunately, this hypothesis can only be directly verified by experiment. We learn causal effects through replication, which involves the use of more than one unit. The way we personally learn from our own experience is to reproduce the same physical object (me or you) with more units in time, making some observations of Y(0) and others of Y(1). When we want to generalize to units other than ourselves, we usually use more objects.

This occurs, for example, in social science experiments with students and possible pedagogical interventions such as value creation assessment (e.g., Rubin et al., 2004). Replication does not help without additional assumptions. The simplest assumption is the stable treatment value assumption (SUTVA; Rubin, 1980, 1990), according to which the possible outcomes for the ith unit are determined by the treatment of the ith unit. That is, there is no interference between units (Cox, 1958) and there are no treatment versions (Rubin, 1980). Then, all possible results for N units with two possible treatments can be represented by an array with N rows and two columns, where the ith unit has a series with two possible results, Yi (0) and Yi (1), each of which could, in principle, be a vector with many components. Obviously, SUTVA is an important assumption. Good researchers try to make such hypotheses plausible when designing their studies. For example, SUTVA becomes more plausible when units are isolated from each other, such as when intact schools are used for units rather than students in schools when an educational intervention, such as a tobacco prevention program, is studied (see Peterson et al., 2000). To solve this problem, we must make some assumptions, because a causal analysis without hypothesis is impossible. If we want the estimator (hat{ATT}) to be equal to the ATT, the selection bias must be zero.

In reality, we will only be able to observe part of the values in Table 8.1. This is the fundamental problem of causal inference (Rubin 1974; Holland, 1986). If Joyce receives the standard treatment, we will observe that she lives another 4 years, but we will not know that she would have died after a year if she had undergone the new operation. We can only observe one of the two outcomes and, therefore, these outcomes are now referred to as potential outcomes. Of course, we do not see any results if the patient is not yet treated. Unfortunately, sequential interchangeability and positivity are not guaranteed in observational studies. Achieving approximate interchangeability requires specialized knowledge that guides researchers in designing their studies to measure as many variables as possible in solution. For example, experts in an HIV study would agree that time-varying variables, such as CD4 count, viral load and other common predictors of treatment and outcomes, need to be measured and adjusted appropriately.

In observational studies, however, the state of sequential interchangeability cannot be tested empirically. As with fixed treatments, causal inference for time-varying treatments requires the unverifiable assumption of conditional interchangeability – only now sequentially during follow-up and not just at baseline. ARC defines causal effects at the individual level. In practice, however, we usually focus on one summary measure: the effect of treatment on the people treated. In this article, we will look at some of the methods commonly used in causal analysis. First, we`ll go over a bit of theory and talk about why we need causal analysis in the first place (the fundamental problem of causal analysis). I will then introduce you to propensity score matching methods that are one way to treat observational datasets.