Sunday, March 3, 2013

Which priming claims conflict with research on subliminal perception?

I've received several interesting responses to my post on the history of disputed claims of subliminal persuasion. Perhaps the most interesting comment, from a theoretical perspective, was the idea that goal priming does not depend on the stimuli being perceived without awareness. According to this view, priming researchers are not actually interested in testing subliminal perception or persuasion. Rather, they are focused on the more traditional idea from social and cognitive psychology that we lack insights into the reasons for our actions; our behavior is influenced by primes that may or may not be processed without awareness, but we are unaware of the influence of those primes. By that view, presenting the primes subliminally is a means to an end, not an end in itself. As John Bargh wrote in 1992"subliminality of stimulus presentation, therefore, is important not because of the subliminality per se but because one cannnot be aware of the influence of a subliminally presented stimulus."

As I noted in my earlier post, claims of goal priming that do not argue for implicit perception are not controversial from a subliminal perception perspective, and implicit perception folks would not necessarily be skeptical of those.  For example, in their studies in which holding a warm or cold drink influences ratings of personality warmth, Williams & Bargh do not claim that the stimulus itself is implicit. It would be crazy to do so—after all, subjects were asked by the experimenter to hold the drink, so they presumably are aware of the drink and whether or not it is warm. Those studies are focused on a more traditional social psychology question: To what extent are we aware of the reasons or mechanisms underlying our judgments, and do those subtle mechanisms have big effects on behavior. That point is not controversial from an implicit perception perspective since there is no claim of implicit perception, but they are provocative for other reasons (see below). 

If all of the social goal priming research were focused on awareness of influence rather than on the subliminal nature of the stimuli themselves, it would not have inspired as much skepticism from those interested in subliminal perception. After all, the idea that we have mistaken intuitions about the workings of our minds is well established in both social and cognitive psychology.

But, many studies in the social priming literature explicitly claim that the prime stimuli themselves fall outside of awareness, and they use the subliminal nature of the primes to argue that the influence of those primes must occur outside of awareness as well. For example, consider these quotes from Bargh et al's seminal 1996 study of age priming (emphasis added):

"this behavior is unmediated by conscious perceptual or judgmental processes" 
"by the mere presence of environmental features, we mean that the activation of the behavioral tendency and response must be shown to be preconscious; that is, not dependent on the person's current conscious intentions."
"Social behavior is like any other psychological reaction to a social situation, capable of occurring in the absence of any conscious involvement or intervention."  
In their discussion, Bargh et al argue that their study was different from the Vicary "eat popcorn" study/hoax  because the behavioral goals were more relevant, accessible, and not in conflict with other goals (like staying in the theater). In other words, the age-priming study worked because it primed more accessible or actionable goals. Although the implicit nature of the prime is not the core issue for this study, and the result doesn't depend on it, the paper does imply that you don't need to perceive a stimulus consciously for it to have an influence. If conscious access to the prime itself is truly irrelevant, why bother trying to hide it in any way? Why measure awareness of it later?

Other more recent studies in the goal priming literature have made far stronger claims that the primes themselves are subliminal. For example, Hassin et al's PNAS paper claimed:

"We report a series of experiments that show that subliminal exposure to one's national flag influences political attitudes, intentions, and decisions, both in laboratory settings and in “real-life” behavior."
If the subliminal nature of the stimulus isn't central to the claims of goal priming, why claim that it was a subliminal exposure? Why bother presenting it rapidly and masking it? This one falls squarely into the much-disputed implicit persuasion literature, and it lacked adequate controls for awareness of the stimulus: it relied on post-experiment questioning to claim that the primes fell outside of awareness, a technique well-known to be inadequate to rule out awareness of the prime. This lack of proper control for awareness, coupled with claims of implicit persuasion, justify the sort of skepticism I wrote about in my previous post. More broadly, claims of subliminal influence like this one are not unusual—they seem to be accepted and grouped together with other goal priming findings in the literature, which leads me to the conclusion that at least some of the goal priming literature is assuming that the primes themselves fall outside of awareness. 

Another theoretical reason for skepticism

Although claims of subliminal persuasion are perhaps the largest reason for skepticism among those who study implicit perception, there are other theoretically motivated reasons to be skeptical of some recent claims that primes change behavior. Again, the skepticism arrises from a difference in the theoretical perspective of those studying goal priming and those studying other forms of priming. This reason has to do with the purported breadth, power, and persistence of the primes. 

Cognitive psychologists tend to think of priming effects in terms of spreading activation: Primes have a larger effect on closely associated representations and weaker effects on more remotely associated representations. Moreover, the activation diminishes rapidly as the associations become more remote, leading to almost no activation with relatively few steps between the prime and the target. Cognitive psychologists see the links between primes, goals, and behavior as remote, and if they are remote, the influence of a prime should be weak rather than strong. In contrast, goal priming advocates argue for a fairly direct link between primes and goals, with activation of goals directly influencing behavior even when people are not aware that their goals have been triggered by the prime. 

Why might cognitive psychologists question the close link between primes, goals, and behavior? Take what is perhaps the strongest and closest form of semantic priming (i.e., priming of meaning): A prime word leads to faster decisions about a closely related word. For example, seeing the word "doctor" leads to faster processing of the word "nurse." Even that closely related prime requires some spreading activation: Seeing the word doctor spreads to other closely related concepts (nurse), but it produces less priming of "nurse" than it does for "doctor." Such identity priming doesn't require as much spreading activation.

The implicit perception literature shows that it is exceptionally difficult to find evidence for semantic priming of closely related words when people are truly unaware of the prime. That was the focus of my last post. Yet, even with full awareness, a prime does not have a huge influence on semantically related words. In a meta-analysis of semantic priming, closely related semantic associates primed judgments about a related word (e.g., is it a word or not) with an effect size of about r=.21 (Lucas, 2000). Contrast that modest priming (with awareness) for closely related words to the much larger effects of goal priming from words to goals to behavior. For example, the reported effect size for the priming effect of warm coffee on personality judgments was approximately r =.3. It seems implausible to those who study semantic priming that holding a warm cup of coffee would have a bigger effect on personality judgments or pro-social behaviors than seeing the word doctor would have on judgments about the word nurse.

Reconciling the size of social priming effects with the apparently smaller size of explicit semantic priming requires one of three possibilities:

  • The chain of associations linking physical warmth to personality ratings is more direct than that between doctor and nurse. That would require a rethinking of the structure of representations.
  • The mechanisms guiding behaviors in goal priming are different from and more powerful than those underlying other forms of priming.
  • The social priming effects are not as large (or the semantic priming results not as small) as the published reports suggest. 
The first two possibilities would be strong theoretical claims that would require a rethinking of decades of priming research and research on the nature of semantic representations. Although they might be true, such strong claims merit skepticism (not dismissal. skepticism). The third possibility merits direct replication with large samples, preferably by multiple labs, in order to better estimate the true size of the effects. If the goal priming effects prove to be smaller than those for priming of close semantic associates, this second theoretical reason for skepticism would be negated (or at least weakened substantially). Given that the third possibility is the easiest to test and would potentially shore up the interesting claims of goal priming, it seems like the right way to go.


  1. "It seems implausible ... that holding a warm cup of coffee would have a bigger effect on personality judgments or pro-social behaviors than seeing the word doctor would have on judgments about the word nurse."

    This is indeed exactly the question I have concerning the social priming literature. Some of the effects seem amazingly large from a cognitive priming perspective. There are at least two methodological differences between cognitive and social priming experiments that are worth considering.

    First, cognitive priming studies have far more trials (usually >16, I'd estimate) than social ones (often only 1) but I don't see how this could explain the social advantage in effect sizes, unless social priming researchers are just a lot better at selecting their stimuli and running their experiments or are just incredibly lucky.

    Second, cognitive priming experiments typically use within-subjects designs and social ones between-subjects designs. Again, right off the bat this doesn't lead one to expect larger effects in social priming experiments.

  2. Hi Dan,
    This is a very nice set of blogs you've written about the subject.
    I am just wondering about one other possibility to explain the difference between the two. What if there is a difference at the measurement level? What if it is actually easier to be persuaded in a personality questionnaire, for instance, to score slightly higher, than to have faster responses in a "doctor -> nurse" semantic priming? There could be two reasons for that, the first is that the measures themselves are not equivalent and that we should test with the exact same type of DV. The second could be that the questionnaire type of study is actually a prime-reinforcing DV in the sense that it obviously points in only two directions (one corresponding with the prime and the second opposing it). The same goes for many of the behavioral outcomes (you either walk the same pace, faster or slower, etc.). In contrast, the semantic priming research seems to use more of an open-ended format that is very similar to the idea of spreading activation: it can go in each direction. After the doctor-prime: you could test for reactions to "nurse" but also "hospital", "medicine", "illness","lab coats", ... As such, it doesn't really funnel the priming into a certain direction that social priming would do.
    I am, of course, not as much an expert on this topic as you are, but I am certainly interested in your answer.

    1. Interesting idea that the priming might be stronger because of the nature of the measurement. The measure is still response time, of course, so the key would be that the priming effect is larger because it can produce a smaller range of possible behavior outcomes. That doesn't really resolve whether the link between the prime and target is more or less direct than semantic priming of a lexical decision. But, as you and Rolf both noted, both the outcome measures and the designs are different in these cases. I think you'd have to argue that the goal priming measure was more sensitive to the prime in order to explain the larger effect sizes, but I don't see why that should necessarily be the case.

    2. Tim, I think this is a very good take, but in the sense that it serves to illustrate why the issue is so confused in the first place. The social and the cognitive approaches seem, for all intents and purposes, impossible to compare directly--different fundamental assumptions, different measures, different theoretical frameworks. If not incomparable, they are at least sufficiently different that we can't say one of them must necessarily be right.

      If I might propose a 4th way to reconcile the findings, it might be to conceive of priming as preparing for action. I think this is theoretically tempting because preparing for action is the implicit link between goal priming and semantic priming: nurses have relevance for preparing to engage in certain actions, and doctors do something similar for many of those. For many actions in practice, a nurse and a doctor are either inseparable or interchangeable.

      Thus, we might conceive of goal priming as an internally oriented form of action preparation, and semantic priming as an externally oriented form, both driven by the same underlying mechanism. Further, this might imply that in the absence of a purpose for action, semantic priming is distorted, and in the absence of sufficiently rich semantic information, goal priming is distorted.

    3. Sorry, that was by Christian Hummeluhr, I'm not sure why it posted as zodium.

    4. Christian -- thanks for the comment. I think you're proposing an interesting variant of the first option, one that requires a rethinking of the nature of representations. Framing all priming in terms of preparation for action would make some of the goal priming links more direct than semantic priming ones, but I'm not sure it's possible to reframe the pattern of semantic priming results in terms of action preparation (e.g., typicality effects don't seem to fall out naturally from an action framing). And, I'm not sure the internal/external split quite captures the distinction. Goal priming work seems to demand some sort of outward action as well, leading to different judgments of people, etc. So, it's not entirely internal.

      I think, for this reframing to work, it would be necessary to posit some sort of representational structure that is organized based on actions rather than semantics. And, whatever structure falls out of that would need to (a) account for the pattern of priming results from semantic priming, (b) account for the goal priming pattern, and (c) show that goal priming representations are closer together in some sense than semantic ones are. That's an intriguing possibility, and it's the sort of theoretical work that I'd like to see. It's necessary to try to reconcile the results and effect sizes from these largely separate literatures.

    5. Thanks for both your replies to my comment. They are very interesting, constructive, and actually much more humane than many of the harsh criticisms we come across on this topic. I would be very much interested to see this stream of thoughts put into research.

    6. Thanks Tim. I think examining the different theoretical and empirical traditions can add insight into why these two fields seem to talk past each other. At least I hope it can. I don't know if there is any straightforward theoretical resolution, but more data that directly address the mechanisms might help.

  3. Hi, Dan:

    As you know, I also take a critical eye to this work. But your logic about the strength of social & goal primes on behavior being constrained by or even informed by the strength of priming effects on spreading activation in a semantic network has hidden assumptions that call it into question.

    Your argument relies on the fact that semantic activation of relevant words is the single underlying mechanism responsible for the effects of social/goal primes. It is not at all obvious that this is the case, and more important, whether you believe this or not depends entirely on your underlying theory. Yes, Bargh in the original 96 work described semantic activation as the entire mechanism for understanding why elderly primes led to slower walking (prime increases accessibility of category-related words, with direct output of that accessibility to behavior). In this model, you are correct that the strength of the prime->behavior effect cannot be larger than the prime->activation of category effect.

    But why should we evaluate the entire discipline based on one (really bad) model? As we've shown before (and as Christian suggests above), there are other ways of understanding priming effects, such as motivated effects, preparing for interaction, etc. And once you allow for this there is absolutely no reason to think that the strength of the prime->category effect should constrain the prime->behavior effect. For instance, suppose priming elderly-related words leads to a short-lived and fairly weak activation of the category "elderly". Then suppose that I really, *really* hate the elderly. In other words, they are very important to me and I have well-practiced responses to them. My self-regulatory systems take over and I walk more quickly to get away from them. Or I absolutely love the elderly, and so I then walk more slowly to be with them. Hence, a small effect of spreading activation can lead to a very large effect on behavior, can it not?

    So the comparison of the strength of prime->behavior effects with the strength of spreading activation effects in a semantic network is meaningful IF AND ONLY IF the mechanism for understanding the former is entirely the latter. (As a side note, you describe the elderly prime effects as something having to do with goals, but I think you undermine your argument in doing so--Bargh never thought about that effect as having anything to do with goals. That work came later, and his explanation of the behavior priming stuff was always amotivational, perception-behavior link, etc. So you give that early work too much credit.)

    I do want to emphasize that I don't think the criticism of this literature has anything to do with "cognitive" people (god, can we please stop making that argument and be a little self-critical!) and I think your analyses are generally right-on. But I do think that when you and others make this argument that "we find effect X is small and temporary, therefore your effect Y must be constrained by our finding" it relies *entirely* on the assumption that your model for effect X is *the correct model* for effect Y. Any other processes at play, and that argument falls apart.


  4. (comment above continued, it was too long for one post!)

    The other thing I take issue with is talking about the warm/cold impression formation work in the same breath as the social/goal priming. My understanding of the coffee cup work is that it's supposedly about "embodiment"--the shared systems underlying physical and social warmth (literally, the shared neural systems). I don't think it's solely about the priming of the concepts "warm" and "cold" influencing impression formation. After all, we've known from Higgins et al. (1977) that primed concepts influence impression formation. (And if you want to talk about a replicable effect, I replicate that effect in my undergrad social class every semester.) So I'm pretty sure that they're doing something more than saying, "we can prime 'warm' and it influences impressions." At least, I *hope* that's true. If it's about something more than the priming of that construct in a semantic network, then as with my argument above, the same thing holds--the comparison of effect sizes is irrelevant here.

    Also, this is Joe Cesario. Don't know why it thinks I'm J&K

  5. Thanks for the comments, Joe. As with Christian's comments, I think what you're arguing falls into that first category of rethinking what representations are affected by primes. And, it's an interesting option. You're right as well that I've clustered together priming findings that probably can be treated as distinct. Priming goals vs. semantic priming vs. embodiment might all involve different mechanisms. The thing that's primed could be different in each case, and the resulting effect sizes could differ as well. Many of the claims in the literature, especially the older ones, were framed as conceptual priming using the same mechanisms as spreading activation studies. And for those, I think it is important to consider the size of the effects relative to the chain of associations.

    I do think the embodiment claims are claims of conceptual priming as well. They are claims about the nature of the representations. As you note, they involve the supposition that physical representations of warmth are closely linked to interpersonal warmth. That's a claim that the representations are closer together, meaning that priming should be greater. And, for those effects to be larger than priming from doctor to nurse, the argument must be that they are closer together than that. Maybe that's true, but it would require a rethinking of the structure of representations. There are a lot of things that could be linked to physical warmth—why should personality warmth be so closely linked that it produces big effects. Why not hot-headedness instead? Are both linked equally closely? If so, why is personality warmth primed? Why is pro-social behavior primed rather than anti-social behavior that you might expect toward someone who is hot with anger?

    In general, I agree with your conclusion that some alternative explanation(s) or model(s) for this range of priming effects is necessary if they cannot be accommodated within the spreading activation framework. And, the sorts of distinctions you raise are a good step in that direction. Many studies in the literature appear to me to be consistent with a spreading activation sort of model (conceptual priming studies) even if others don't (some stereotype activation studies, perhaps goal priming, maybe some of the embodiment claims). That said, I don't see much criticism within the literature of claims that fall directly in the spreading activation model but produce effects that are much bigger than doctor-nurse. I don't see much criticism of claims of subliminal priming on concepts and behavior from those who don't think making the primes subliminal is important. These effects are all often cited together as mutually supporting, leading to them being grouped together (perhaps erroneously) boh in and out of the literature.

    1. Dan and Joe, thanks for your replies. I think Joe is spot on in pointing out (or at least I think he's pointing out) that your criteria for explanatory success do seem to implicitly favor the prevailing explanations. An effect size argument can provide crucial information, provided we are confident that these different frameworks are engaged in studying the same physical process (I am not, because they are not easily compared), AND that we are confident at least one of the frameworks is appropriate (I am not). The trouble with the effect size approach is that I don't think we are in the business of making objective estimates of any explanation's truth value or comparisons in the space of all possible explanations, but rather of making subjective comparisons between specific, explicitly proposed explanations.

      So, while I can see how it might be interpreted that way, I don't think my proposal necessarily implies rethinking the nature of representations--it would be more accurate to say I'm questioning the fundamental role of representations in priming, more a type of Gibsonian/ecological argument than a twist on the same fundamental spreading activation model. I suppose in some sense we could say this is rethinking the nature of representations, but it seems like a bit of a stretch.

      The replacement structure I would propose is something at least similar to that of affordances: doctors and nurses afford many of the same behaviors, so preparing for action oriented toward one will effectively be equivalent to preparing for action oriented toward the other, even if you are only actually exposed to one. I'm not nearly as steeped in the priming literature as Daniel, so I'll take his word that the internal/external dichotomy is not helpful for explaining priming. I think, however, that some of the confusion surrounding the issue reflects a need to reconsider these categories in the priming literature, such as liminal/subliminal.

      (While I'm sure cognitive, social, and ecological psychologists will all take simultaneous issue with my use of affordances here, I'm only using it for illustration of a radically different framework to base explanations on, rather than any specific explanation.)

    2. Hi Christian. Thank you for continuing this interesting dialogue, and sorry it took me a day to get back to you. I'm not sure I follow your argument about not being in the business of making objective estimates of any explanations truth value. I think that's exactly what we're in the business of doing, at least in terms of measuring the objective size of actual phenomena or effects. You're right that quantifying the "truth value" of different explanations of those effects is a different enterprise, but evaluating the actual sizes of the effects is crucial. And, the actual size of the effect can be informative when we do have knowledge abou the typical effect sizes produced by various mechanisms. I had argued that these effect sizes were implausible for a mechanism that relies on spreading activation of semantic information. That led you and Joe to argue that the mechanism involved is something different. That seems like a reasonable case to make, but it depends on that effect size being implausibly big for the mechanism I typically think of to explain these sorts of effects.

      I'm also not sure I buy your Gibsonian-style argument here (speaking as someone who did his grad training at Cornell and came from a Gibsonian perception tradition). I guess I don't see that the word doctor affords any particular action at all (other than reading). And, even seeing a physical doctor doesn't necessarily afford the same actions as toward nurse. That's a semantic relationship, not a perceptual affordance one. That said, reframing representations in terms of actions is a rethinking of the nature of representations. Gibson was famous for arguing that representations aren't necessary for perception. That too was a rethinking of representations (a more radical one than I think you are proposing here). I do think a bit more thought is needed to put these sorts of priming effects into an action framework. It's not clear to me that doctors inherently afford the same action preparations as nurse (any more than they would for any human). The similarity with which we act toward doctors and nurses depends on the semantic relationship between our representations of doctors and nurses (what do doctors do? how is it similar to what nurses do?). Action could be a part of those semantic represnetations, but for doctor to prime nurse, you still need a semantic network with representations of each, and you still need to account for the distance between them in some sense. It's hard for me to see how you attach action plans to such a representation in a way that would make these sorts of effects parallel to other sorts of priming effects.

      I think a better route is suggested by the first part of your comment: Frame these effects in a different way, using a different mechanism, one that is commensurate with the size of effects that we tend to observer. I'm just not sure I get what that mechanism is and how you can get away from the need for spreading activation across semantic representations of some sort.

  6. regarding hot coffee vs. the word doctor.

    hot coffee is a visceral experience. which is a different kind and level of effect.

    Indeed, without much knowledge, I think that affect is way stronger and wide spreading than words and cognitive concepts.

    1. Hi Joe. That seems like a completely different mechanism than is typically proposed for such effects, but I could imagine it giving a better accounting for the effect. For example, perhaps holding something warm just makes us feel happier, and when we're happier, we rate people more positively and we're nicer to others. That seems reasonable enough, and I could imagine such an effect being larger than a spreading activation effect. But at some level, it's also less interesting than the claim that physiological warmth is associated with interpersonal warmth because they share a conceptual space. It also suggests a need for different sorts of studies. For example, would a mood induction yield the same pattern of results? If so, then the result has nothing to do with the concept of warmth at all. Would hot coffee yield more positive ratings on other dimensions? It should if it's a visceral, affective link rather than a conceptual one. It would be interesting to look at the typical effect sizes for mood on personality ratings.

  7. Hi Dan,

    Thanks for the comments. In general, I agree with many of the things. As I noted elsewhere though, if the effects are indeed social (which I think they are), I'd say they should be more motivating than a 'simple' semantic prime. The argument relies on many earlier accounts (e.g., by Bowlby and others). However, as many others mention here as well, a visceral experience could produce stronger effects than semantic primes (think of the work by Rosch in the 70s, where verbal couplings produce slower response latencies than visual ones).

    In addition, the positive valence does not seem to account for the effects. We don't find it (implicitly, explicitly - believe me, I tried). Others don't find it either (even when they expect it, see e.g., Kolb et al.). So, mood does not seem to account for the effect. We seem to find these effects also early with young children (and, we think they may respond to warmth prosocially even earlier). Nevertheless, I checked for some of my effect sizes and they seem to be around r=.17-21 in some of the studies (but they get a bit more substantial when I measured it somewhat more implicitly, such as through language use). In a more recent study that we are still writing up though, we do find (of course) that 'known' friendship relations produce stronger effects than a 'simple' warm prime. Perhaps that helps in interpreting?

    This does also not mean that the warmth priming should only have its effects on prosocial behavior, but effects have indeed been found on anger as well. This should not be surprising, as Ekman has linked ANS activity/skin temperature also to different types of emotions. Also, within other literatures, a clear link has been made from touch -> skin temperature/stress. I personally believe that the anger effects are then so activated because of different types of conceptual processes that are being activated. The Anderson studies, if I recall correctly, besides having a relatively high (irritating) temperature, also show participants stimuli that are already hostile (and may thus evoke specific behaviors).

    Finally, Bargh has not really been the only one obtaining such effects, and if one wants to review/replicate the warmth work (which I hope folks will do), then one should look elsewhere as well.

  8. Hi Hans. Thank you for the detailed comments. You might well be right that "social" primes are inherently stronger than simpler semantic primes, although I would like to know what mechanisms in particular make them stronger and how the representational structure differs from other forms of semantic representation. I guess it's not clear to me what it means to be visceral and how such visceral connections would lead to stronger effects. That does require a different mechanism, perhaps some way of strengthening the weights between concepts or a more direct pathway for priming to induce its effects.

    Interesting that mood or positive valence doesn't induce the same sort of effects. That does seemingly eliminate one possible alternative pathway that wouldn't need to operate by spreading from one concept to another (prime -> positive affect - > generalized positive responding). I guess what I haven't seen yet (and that's probably due to my own lack of expertise in some of these areas) is a structural/mechanistic explanation for how these priming effects operate and what sorts of pathways or concepts are being primed. How are these concepts represented and how are those representations connected such that priming has predictable effects. Without such a model, it's tough for me to wrap my head around how a warmth prime could lead to increased prosocial behavior increased anger (maybe that's with different primes). I'd like to see a more mechanistic account that spell out each step in the process from prime to outcome. That would also help differentiate the effects from the sorts of semantic spreading activation effects I mentioned.

    For what it's worth, I only mentioned the Williams & Bargh finding because it was the one I had seen (it was in Science and is cited a lot). I didn't intend to neglect others in that field - I just used it as what I saw to be an example of claims of conceptual priming. I imagine there are many others I could have used in its place.

  9. Hi Dan,

    Thank you as well for the detailed comments. Let me make another distinction. I think that for many of the embodiment effects we can make broad distinction between two types of effects - similar to many other effects in cognition: top down and bottom up. Many of the top down effects may fall in the view that some have argued as conceptual metaphors/metaphoric transfer. I'd think that these are far more bound to context (e.g., the link between time and space, which has also been suggested to be moderated by culture).

    The work that we have been working on should be closely linked to ANS functions and oxytocinergic effects. We have found one link with skin temperature (i.e., social exclusion leads to lower skin temperatures and warmth mitigates the effect). We are trying to work out these effects beyond these relatively simple 'priming' effects (if one still wants to include it as priming, if it is simply vasoconstriction/vasodilation). It does not mean that there are no top down effects (e.g., through internal working models, see Fay&Maner, and our own work with children), but the most basic effects are also obtained with young children (e.g., young infants are soothed by warmth when they are stressed as well, more so than a pleasurable treatment with sucrose).

    There are a whole bunch of these converging effects (see for example the problems oxytocin deficient mice have in regulating temperature, oxytocin promoting heat transfer in mammals when feeding pups, and oxytocin-thermoregulation links in humans), but I agree that the full mechanisms are not clear yet. But that's ok, it's ambitious to do so and I think progress is being made. Forgive the blatant self-promotion, but the working out of mechanisms is something that we will try to invite here:

    As a 'primer': we are working to include a 'registered reports' section, based on what Chris Chambers proposed at Cortex, which I hope will increase the confidence in these mechanisms/effects.

    1. Thanks Hans. No problem about the self-promotion -- great to let people know about that sort of special topic. I'm not sure I completely follow the top-down/bottom-up distinction you've drawn here. I don't tend to think of priming effects as top-down at all, and they typically are described as automatic, which implies a more bottom-up or obligatory process rather than something guided by intentions. The idea that physical warmth triggers some sort of regulatory processes seems reasonable. What I'd like to see is a more specific explanation for how those regulatory behaviors then lead to pro-social behavior or judgments about the warmth of another's personality rather than to the many other things they could do. More broadly, if physical warmth leads to such behaviors and judgments, are people in warmer climates inherently more charitable? Do people living in cold places think everyone is cold? That doesn't seem quite right to me. If not, is it the relative change in feelings of warmth at that moment? If so, would people be more pro-social right after walking outside on a warm day? What are the constraints of these effects? What are their limits? Knowing more about the hypothesized chain of "events' that leads from the prime to the outcome would help in better understanding these effects.

  10. Sorry, I do tend to get lost in the regulatory work, given that I think it's the more exciting avenue now. Regarding the automaticity part: I myself am not really joined to any automaticity claim. Such responses may well be controllable given specific conditions and depending on the representation. I do really like the questions that you are asking though.

    The distinction to me seems to rely more on the type of representation, which may be one assumption that may be different. The level of representation is not necessary a semantic network type of representation. In fact, many people have stressed that representations may rely on soft versus hard interfaces (Zajonc) or "simulations" (Barsalou). This is an assumption in many of the embodiment work (although the radical embodied people would disagree). So, Zajonc and Markus for example talks about manipulating heart rate that would also differ the way people operate in specific behaviors (I cannot remember the specific DV there). The same would hold for the specific work we talk about here.

    My approach to date has been mostly relying on descriptions from other theories. That is, warmth seems to evoke a communal sharing mindset (one of Alan Fiske's relational models), which generally lets people engage in trusting relationships (akin to mother-infant relationships, those between romantic partners, and so forth). Warmth (as related to touch) should be one of the early cues for preverbal infants to interpret the environment as safe and trustworthy (in another relational model, authority ranking, preverbal infants seems to associate dominance/submission with power - see Lotte Thomsen's work).

    Now, it is not the case that just anybody comes to associate warmth with a good quality relationship (in which generosity is afforded). In fact, we find that those children who do not associate physical warmth with good quality care (i.e, insecurely attached) do not become more generous (you do see the effect for those who associate good quality care with warmth - securely attached). Is this relying on semantic networks? I doubt it, so the nature of the representation is different (and "priming" of warmth in this case may well be different). However, it is true that people have started to tease apart these mechanisms already to some extent.

    Ainsworth also stressed early on as well that mothers of avoidant children tend to be more reluctant to touch. So, the effects of warmth should be primarily geared towards "something" about touch, close proximity (and probably also specific types of smells related to the mother-infant interaction). Warmth just seems to be the most dominant of these, because throughout evolution, it should have been associated with all of the most dominant communal acts (like sex, sharing of fluids, providing care for an infant).

    That basically also means that this is really not directly related to climatic differences. Climatic differences and differences in national culture are far more complex. That is, in warm climates people come outside far more frequently, they should interact more, have different baselines for temperature. There should be SOME relation, but it's a lot harder to tease apart (we did find effects of a warm room on feelings of closeness, but again, this is an incidental manipulation, and not a climatic difference). For what it's worth, we did do an analysis of an existing dataset, but the effects seem to be quite instable (paper is still under review:

  11. Hi. Dan, I'm not sure if you're still reading this older thread (which I just saw), but here's another perspective on "Reconciling the size of social priming effects with the apparently smaller size of explicit semantic priming". I wanted to address this issue more generally than some of the past comments (though these thoughts aren't inconsistent w/ some of the other posts).

    Several people I respect (including you and Hal Pashler) have recently been making this general argument: if phenomenon X depends on phenomenon Y, then the measured effect size of X shouldn't be bigger than that of Y.

    I completely fail to understand this argument; it seems like a non-sequitur to me, so I must be missing something. In general, the measured effect size of any phenomenon will be a function of both (1) the underlying phenomenon itself, and (2) the task used to measure it. As a result, you can take the very same phenomenon, and reliably get two very different effect sizes as a result of measuring it with two different tasks. (In vision, e.g., take the phenomenon of object-based attention; here you'll reliably get a smallish effect size if you measure it w/ spatial cueing, a medium effect size if you measure it w/ divided-attention tasks, and a larger effect size if you measure it w/ something like multiple-object tracking.) It's presumably the same effect in every case (since we care about underlying processes in the mind, not paradigms used by scientists), but that effect gets filtered through different task constraints.

    So the real form of your argument, though it's not stated as such, must be: if phenomenon X depends on phenomenon Y, then the measured effect size of X as measured with task A shouldn't be bigger than that of Y as measured with task B. But that certainly doesn't follow, since B could itself constrain the effect size much more than A.

    Back to the actual topic being discussed: semantic/associative priming in cognitive psychology has typically/historically been measured w/ piddly little fast-response-time tasks (a la lexical decisions) that allow room for effects of only a few 10s (or 100s at most) of milliseconds -- such that you'll probably never be able to get a huge effect size, regardless of what you're measuring. This isn't because the underlying process of spreading activation is weak; it's because the bottleneck through which you're measuring it is weak. But many of the 'social priming' phenomena are measured with tasks that themselves allow for much more variable performance (even when measuring "response" time -- e.g. when the response is the time taken to walk down the hall), and so it's not unsurprising that the measured effect sizes would be much larger, even if they depend in part on some of the same underlying processes. (And I think this is a larger sociological difference between the two fields: relative to cognitive psychologists' tasks, social psychologists' tasks tend to be much harder to pin onto specific underlying cognitive processes, but they're sooooo much better suited for yielding huge effect sizes.)

    In short, if task A is a great task with lots of room for variable performance, while task B is a crappy and highly constraining task, then you can easily get a larger measured effect size for X than for Y, even if X depends on Y.

    In other words, vis a vis "Reconciling the size of social priming effects with the apparently smaller size of explicit semantic priming": there's really nothing to reconcile in the first place, either in this specific case or in general. The only rare context where that argument might work would be if the paradigms were identical...

    What am I missing?


    1. Hi Brian (I assume),

      You're missing a couple things, I think :-).

      1) Your description of my premise isn't quite right even if the logic of what you say mostly is. You state "If phenomenon X depends on phenomenon Y..." - The real question is more of the following form:

      If both X and Y operate via Mechanism Z, and X requires more steps in Mechanism Z than does Y, then then X should be a smaller effect than Y."

      If you think of this in terms of classic subtractive logic, each additional associative link should have a cost, meaning that a more remote associate should produce smaller effects than a closer associate. In classic spreading activation form, seeing "robin" primes "bird" more than it primes "animal" because you have to go through more steps to get to animal. More remote associates produce smaller priming effects.

      In the case of some of the priming research, some cognitive psychologists wonder why the effect sizes for conceptual social priming (warm cup primes concept of warmth which spreads to related meanings of warmth which then spreads to pro-social behavior) should be bigger than conceptual priming for much more direct semantic associates. It shouldn't if the mechanism works the same way. That's an argument for why a different mechanism would be needed to produce larger effects, and some of the folks commenting on this post have suggested such alternatives.

      2) Your arguments about different measures being differentially sensitive to the same underlying mechanism is a good one. Some measures are more sensitive than others, and that might account for differences in the size of the obtained effects. For that logic to hold, though, you would need to make the case that a single-trial measure produces a more reliable result than an average across many trials. As someone who does a lot of single-trial studies, I'm not sure I'd go that route. In essence, you'd have to argue that the dependent measure used in social priming research produces a more *reliable* measures of the underlying mechanism. I think that will be a tough sell with a single-trial measure. Tasks with multiple trials might be a better case for this sort of argument.

      Continued in next reply...

    2. Continuation of last reply...

      3) Your argument about effect sizes is wrong, though. I think you're conflating nature of the dependent measure with the size of a measured effect. A more variable outcome measure should lead to *less* reliable effects which in turn would lead to smaller *effect sizes* even if it leads to a bigger absolute measure. Walking down the hallway is measured in seconds whereas lexical decision is measured in 10s of milliseconds. That doesn't mean walking as an outcome measure will produce a larger effect size. For example, walking would be a much worse measure of lexical priming (walk to door 1 for word and door 2 for non-word) -- your latencies would be much longer and more variable, but the variability would swamp whatever mechanism contributes to a difference in lexical decision times (because that mechanism operates on the level of 10s of milliseconds).

      The big advantage of using such controlled, boring measures is that they can produce a more reliable estimate of differences across conditions. And, more reliable estimates produce bigger effect sizes for a given difference between conditions. So, the fact that walking down the hallway has greater room for variability does not necessarily mean you'll get a bigger effect. You might, if the mechanism underlying the effect operates on a scale of seconds. But, most models of spreading activation don't operate on that scale.

      If you want to make the argument that the social measure allows for bigger effect sizes, you would need to make the case for a different mechanism, one that operated on the scale of seconds rather than 10s of milliseconds. That might well be the case for these sorts of social effects, but it could no longer be explained by more typical mechanisms for conceptual priming and spreading activation. That's why I argued that some other mechanism would be needed (or a complete rethinking of the mechanisms for spreading activation).

    3. Hi Dan. Thanks for taking the time to help clarify these things for me; your response makes a lot of sense, and is very helpful.

      I still think that these discussions of what we might call "effect size chaining" can't make sense unless we always take the dependent measures into account in an explicit manner. To the extent we differ on this at all, though, this might just be an issue of rhetorical style rather than logical substance.

      I guess I can't really comment on social priming per se, since I don't know much about that (and I wasn't even paying attention to the single-trial vs. multiple-trials issue, on which a bit more below). But I think that this issue can be sharpened even within the realm of semantic priming itself. Imagine that you had two tasks for measuring semantic priming, one of which was pretty good and one which was pretty crappy (either swamping the effect w/ independent variance [per your points about "walking" dependent measures] or simply not allowing for much mechanism-related variance in the first place). (I'm not sure what the good measure would be -- maybe some variant of stem completion? -- but the crappy measure might be a timed lexical-decision task.) It seems to me that you could easily end up with a situation in which the robin-priming-animal effect size (as measured with the good task) was larger than the robin-priming-bird effect size (as measured with the crappy task) -- even though you were studying the same "mechanism" in each case.

      In other domains that I know even better, I'm sure that you could have this situation. For example, object-based attention effects are larger and more reliable when the 'objects' in question enjoy properties such as closure. But if I measured OBA for closed objects in a spatial cueing task but OBA for un-closed "objects" in a divided attention task, then I could easily get a larger measured effect size for the latter. The reason is that RT-based spatial cueing tasks ("press a key as soon as you see the probe") allow for relatively little task-related variance, since the speed w/ which you make a detection response is just never going to be that slow or that fast; you'll end up w/ an effect magnitude of a few 10s of milliseconds at most, and you'll rarely be able to experimentally discriminate effects of different strengths, etc. Meanwhile, an accuracy-based divided-attention task ("press one of two keys to tell me if the two quickly-flashed probes were the same or different") allows for much larger differences, for differences of different magnitudes to be compared, etc.

      Your point about "walking" is well taken: a measure that allows for more variance *unrelated* to the mechanism we care about will be worse and will yield a smaller measured effect size. (And yes, we agree that walking wouldn't be a good measure of semantic priming itself!) But tasks can and frequently do also differ in terms of how much variance they allow that *is* related to the mechanism that we care about -- with more variability of that sort implying a better task and perhaps a larger resulting effect size. So yes, we want "controlled, boring measures" -- but even so, some controlled boring measures are better (and will produce bigger effect sizes) than others. (Back to OBA: your point about the disadvantages of single-trial measures are well taken, but this is a domain where e.g. I can probably get a larger and more reliable effect in a 3-trial MOT experiment than I could in a 30-trial spatial-cueing experiment.)

    4. (Continued)

      So in the end, measured effect sizes will be influenced by many factors, including (1) the "# of steps" in the underlying mechanism (i.e. what you were focused on in the original argument about priming), (2) the degree to which the dependent measure allows for mechanism-related variability, (3) the degree to which the dependent measure allows effects to be swamped or masked by mechanism-unrelated variability, and (4) the # of observations per subject, etc. Reasoning about "effect-size chaining" (a la your "If both X and Y operate via Mechanism Z...") is only possible when you think that the influence on the effect size of #1 is going to swamp differences related to #2 and #3, etc.

      Thanks again,


    5. Oh, and: the only remaining question I have about the social priming discussion itself has to do with timing. You noted that: "If you want to make the argument that the social measure allows for bigger effect sizes, you would need to make the case for a different mechanism, one that operated on the scale of seconds rather than 10s of milliseconds." Must one appeal to a different underlying mechanism simply because the task itself operates on a longer time-scale? Does the timing of different mechanisms even have to enter into such a discussion? For example, could we have a measure of priming that wasn't time-based at all (e.g. stem-completion), but that still yielded larger effect sizes than an RT-based measure (e.g. lexical decisions)? And in that case, might the two tasks be tapping the very same underlying mechanism of spreading activation, even though the former operated on a scale of seconds while the latter operated on a scale of 10s-of-milliseconds? (I'm obviously not suggesting this is the case w/ the walking research, so that this might all be beside the point for the specific discussion about priming that you're having. But again, I'm more interested in the general form of these arguments.)

    6. Hi again, Brian. Thanks for the further thoughts. I think we mostly are in agreement on the logic of the argument, especially the idea that different tasks may produce more sensitive measures of the same underlying mechanism (in the the technical sense of bigger signal to noise ratio), and that more sensitive measures will yield bigger effect sizes. I think the reason cognitive psychologists have been skeptical of some of the large effect sizes for conceptual priming is that the measures do not appear to be the sort that would yield greater sensitivity to spreading activation (e.g., single trials with long response latencies and presumably a lot of variability) and, at least on the surface, they seem to require more steps for the semantic link between the prime and the behavior. Much of the discussion earlier on this thread focused on ways in which those assumptions might be wrong, mostly by arguing that the priming does not operate via a straightforward set of semantic associations. That is, most of the interesting alternatives have involved alternative mechanisms or pathways. I think that's a reasonable way to go, because it doesn't seem plausible that these outcome measures will be more sensitive than more traditional measures of spreading activation.

      If there's one thing you can say about cognitive psychology it's that researchers tend to focus extensively on optimizing tasks. Sometimes, they lose sight of the phenomenon of interest and just study the task itself. After about 50 years of research on semantic priming using various lexical decision and other tasks, I'm willing to wager that the sensitivity of those measures would be pretty hard to beat. Of course, it's possible that the literature has become myopic and missed what might be far more sensitive measures. I'm just guessing that's unlikely here.

      If that's true, then it would be surprising to find a one-trial method that leads to substantially greater effect sizes for the same sort of underlying mechanism. That's why the sort of effect size comparisons seem valid and why some other sort of mechanism would seem to be a more plausible way to explain these sorts of effects. They're easier to accommodate (and justify less skepticism) if the don't operate using the same mechanisms of semantic priming studied using other (presumably more sensitive) cognitive tasks.

      On your broader question: You're right that, in principle, the same mechanisms could produce effects at multiple time scales. In the case of spreading activation and semantic priming, the effects tend to get weaker with longer delays and with more links in the chain of associations. And, it would be surprising to get stronger effects with longer time lags and more links in the chain. I think the reasons to appeal to a different mechanism (or at least a different or more direct pathway or outcome) comes more from the points above, but in this case, time scale contributes to the argument because of what we do know about the time scale of semantic priming of this sort. It's an argument that's specific to this particular issue and not one about timing in general.