Response to Limanowski

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).