Marcin Miłkowski

In his detailed response (https://jakublimanowski.com/comment-on-litwin-and-milkowski/) to our critical evaluation of the study by Limanowski and Blankenburg (2015), Jakub Limanowski (henceforth, JL) claims that our critical analysis is largely driven by misinterpretation of their results and the DCM framework. Below, we provide a point-by-point reply to the issues raised by JL. 

To make things clear: we did not intend to present this study—which is driven by precise methodology and exhibits strict computational rigor in the study of neurocognitive mechanisms underlying body attribution processes—as an example of a bad scientific practice in general. What we meant (and we firmly maintain our opinion after reading the commentary) is that the study design precluded the possibility to interpret its results either in favor or against PP. In other words, while it certainly contributes to our understanding of neurocognitive mechanisms of body ownership, it has absolutely nothing to say on whether these mechanisms are predictive as envisioned by PP. Yet, it is cited as providing direct empirical support to PP (Tsakiris, 2017) and the wordage in Limanowski and Blankenburg (2015) is responsible for this situation. In this response, we shall try to make our points even clearer.

1. Indeed, we interpreted negative values of intrinsic connections of each node as “attenuation of intrinsic connectivities in both the LOC and SII”. We admit that, if our interpretation is incorrect, it renders the part of our analysis pertaining to inconsistencies between two PP models of RHI problematic. However, it also means that the graphical presentation of DCM results is quite confusing. The intrinsic connectivities, unlike others, are bold, which suggests that they “mark significant connections or modulations” (Fig. 6, p. 2297). Similarly bold endogenous connectivity patterns from IPS to LOC are interpreted as “enhanced top-down attention to the visual modality” (p. 2301) irrespectively of the experimental condition; therefore, our interpretation of attenuated intrinsic connectivities during RHI elicitation (in all conditions) seemed warranted.

1. We disagree that this claim is false, but perhaps we could have written that “effective connectivity from IPS to SII was not significant” rather than “altogether absent”. Still, our argument holds: the study provides no evidence for enhanced endogenous connections from IPS to SII in neither of the conditions (palm/forearm/both), which means that they are either non-existent or of negligible strength (+.07) as compared to top-down connectivities from IPS to LOC (+.41, significant; both coefficients derived from the ‘palm’ condition). Therefore, one cannot simply say that “these values were just lower”. It means that there is no evidence that effective connectivities from IPS to SII were strengthened during RHI elicitation (either via synchronous or asynchronous stimulation). This renders the following interpretation of the results unlikely: “IPS would also signal these “adjusted” predictions to the SII, where they do not match the incoming somatosensory information (i.e., the proprioceptive information about the position of one’s real arm and the skin-based information about touches on it), and hence generate another (somatosensory) prediction error” (p. 2300-2301). How could ineffective top-down connectivities drive somatosensory prediction errors? Why there are no differences in their strength during synchronous stimulation as compared to the control condition in which RHI does not occur? This is not discussed in the article. It seems to us that multisensory integration hypothesis sounds not only more parsimonious, but also much more consistent.  

1. In his response, JL convincingly argued that one cannot speak of theoretical inconsistencies if important methodological differences between the studies are present (e.g., different regions of interest are specified), and we agree. Note that, in the article, we explicitly point this out. However, this would not apply to attenuated intrinsic connectivities in particular nodes, which could not have resulted from enhanced top-down attention to these areas, given that in PP 1) attenuated intrinsic connectivities = lower precision (Zeller et al., 2016) 2) attention = higher precision (Hohwy, 2012). This would be the case of inconsistent interpretation of the same observables in one theoretical context. However, if attenuated intrinsic connectivities were actually not observed, our critique does not apply. 

1. What is discussed at length is the PP-based interpretation which, we believe, is accurately summarized in our paper. Basically, intersensory conflict between touch represented visually on a dummy and felt on one’s real arm is supposed to elicit ‘visual’ prediction errors. However, these are the very errors that actually have to be resolved (explained away) for the illusion to arise, according to PP interpretation. In other words, they should accumulate prior to the occurence of RHI and should be absent during the full-blown RHI experience (when somatosensory coordinates are already switched to a visual reference frame). 

This is not necessarily a drawback given that JL and Blankenburg were interested in the dynamics of RHI. Actually, this is a testable hypothesis that could differentiate between PP and simple multisensory integration theories: Would one expect bottom-up effective connectivities from LOC to IPS to subside in a time bracket when RHI is already present? However, in its published form, the study is non-diagnostic and the PP interpretation is likely false.

It actually occurred to us that JL did not relate to other problems raised in our paper; perhaps, more importantly, “one could also expect top-down modulations suppressing errors in perceptual areas to come forward” (see our point 2. above). This issue, problematic for PP, certainly deserved some discussion. 

1. We cannot help but see this PP interpretation as post-hoc, especially if, as JL writes, he “never set out to ‘test PP’ in this study”. We appreciate the usage of non-definitive terms, although, frankly, we consider it to be a rhetoric moderating the impression of an over-confirmatory research strategy. Additionally, in our opinion, it does not matter where the interpretation is introduced exactly, but how thoroughly it is discussed (one and a half page + abstract vs five lines of discussion of an alternative, much simpler explanation which fits the data at least equally well). We also disagree that “it is allowed to [focus on a favorable interpretation] in a Discussion section of an empirical paper” if one does not have arguments for the advantage of this  interpretation at one’s disposal. But what is most important here, again, is that “a body of data cannot provide evidence for a theory only in virtue of its consistency, [but it] must also weigh against the competing hypotheses”, and that “what matters for evidential support is whether the model actually fits the data better than alternatives”. This was simply not shown in the study. Thus, while the study extends our understanding of brain dynamics underlying body ownership processes, it is non-diagnostic regarding whether predictive processes drive the dynamics, and the interpretation of “these results as support for a predictive coding account of hierarchical inference in the brain” (p. 2285, our emphasis) is unjustified. This is actually consistency fallacy at work.

To sum up our main points:

1. The study did not specify 1) outcomes incompatible with PP, 2) outcomes compatible with PP and incompatible with alternative theories, or 3) outcomes incompatible with PP and compatible with alternative theories. As such, it cannot provide evidential support for PP. PP-based interpretation could only be speculatively discussed among other options, especially that there are good reasons to believe that the alternative explanation fits the data better (no effective top-down connectivities during the illusion) and is much more parsimonious. Thus, the gist of our critique is still valid.
2. If the attenuated intrinsic connectivities were not observed, our analysis of inconsistencies between models developed by Limanowski and Blankenburg (2015) and Zeller et al. (2016) does not hold. However, our misinterpretation is at least partially caused by the form of presentation of results in Limanowski and Blankenburg (2015). 

Source: Cognitive Science in Search of Unity

Predictive processing (PP) theory of cognition claims that nervous systems continuously try to anticipate their sensory inputs, following the imperative to minimize the mismatch between their predictions and sensory activations. In the process, the internal model of causal dependencies underlying sensory signals is developed and refined. The theory has recently sparked great hopes that it will provide a unifying account of the entirety of human and non-human cognition: In this view, virtually all cognitive processes are guided by the predictive nature of the internal model. In our recent paper (written by myself and Marcin Miłkowski) we argue that this enthusiasm is premature: PP faces serious problems which effectively stunt its development as a scientific theory. The paper was recently published in the journal Cognitive Science and is now available in open access. It is our second criticism of overextending PP (the previous one is a commentary in BBS on Gilead et al. model of abstract thought).

Our skepticism is based on two main observations. In the first part of the paper, we focus on the “theory-implementation gap”, i.e., the gap between an elaborate mathematical apparatus and its interpretation in terms of psychological phenomena or neurobiologically plausible cognitive architectures. While the formalization of PP is quite strict (but also, notably, very diverse, as there are many different PP algorithms), the theoretical interpretation of its core terms seems to be free-for-all. For example, precision—a concept related to the variability of the signal; thus, to the computational “confidence” or “trust” in its reliability—is being identified with many distinct cognitive and psychological phenomena, including subjective feelings of confidence or trust. This observation applies also to other core technical PP terms, such as predictions or beliefs. Explanations based on such identifications are non-informative, as they are based on the fallacy of equivocation—the confusion of several meanings of a single term in an argument. The theory-implementation gap surfaces also in the computational models of psychiatric phenomena, which do not abide by the root commitments of the theory, regarding functioning and structure of the predictive model.

In the second part of the paper, we present arguments that PP models are not validated empirically in a sufficiently rigorous manner. The vast majority of PP modeling work takes the form of theoretical re-descriptions of contemporary models. These accounts neither yield new, testable predictions nor enable new inferences on phenomena being ‘covered’; they simply use generic PP language to rephrase existing models in hypothetical predictive terms. Moreover, PP proponents harness certain argumentative strategies to conceal the limited usefulness of their models which are often defined as “starting points”, to be empirically validated in the ‘foreseeable’ future. However, they almost never are; instead of testing them against viable alternatives or outcomes explicitly incompatible with the theory, proponents of PP succumb to consistency fallacy, taking selected (broadly consistent) evidence as ‘providing support’ for PP. Not only such practices do not corroborate the theory, but, as we show in the article, they also lead to mutually exclusive PP models of the same phenomenon and wishful interpretations of the obtained data (even in cases when they seem to undermine PP). 

The upshot is that, as for today, PP is definitely not a great unifying theory it was promised to be and its development is arrested. In particular, it displays two features that unifying theories should not possess: It is heterogenous and unsystematically applied. Numerous diverse interpretations of technical terms result in mutually exclusive accounts of the same phenomena or theoretical and computational models being at odds with theory’s fundamentals. Therefore, PP is either underspecified or contradictory itself, but it is certainly not unifying.  

Source: Cognitive Science in Search of Unity