Gi-Yeul Bae and I have previously shown that the ERP scalp distribution can be used to decode which of 16 orientations is currently being stored in visual working memory (VWM). In this new paper, we reanalyze those data and show that we can also decode the orientation of the stimulus from the previous trial. It’s amazing that this much information is present in the pattern of voltage on the surface of the scalp!

Here’s the scientific background: There are many ways in which previously presented information can automatically impact our current cognitive processing and behavior (e.g., semantic priming, perceptual priming, negative priming, proactive interference). An example of this that has received considerable attention recently is the serial dependence effect in visual perception (see, e.g., Fischer & Whitney, 2014). When observers perform a perceptual task on a series of trials, the reported target value on one trial is biased by the target value from the preceding trial.

We also find this trial-to-trial dependency in visual working memory experiments: The reported orientation on one trial is biased away from the stimulus orientation on the previous trial. On each trial (see figure below), subjects see an oriented teardrop and, after a brief delay, report the remembered orientation by adjusting a new teardrop to match the original teardrop’s orientation. Each trial is independent, and yet the reported orientation on one trial (indicated by the blue circle in the figure) is biased away from the orientation on the previous trial (indicated by the red circle in the figure; note that the circles were not actually colored in the actual experiment).

These effects imply that a memory is stored of the previous-trial target, and this memory impacts the processing of the target on the current trial. But what is the nature of this memory?

We considered three possibilities: 1) An active representation from the previous trial is still present on the current trial; 2) The representation from the previous trial is stored in some kind of “activity-silent” synaptic form that influences the flow of information on the current trial; and 3) An activity-silent representation of the previous trial is reactivated when the current trial begins. We found evidence in favor of this third possibility by decoding the previous-trial orientation from the current-trial scalp ERP. That is, we used the ERP scalp distribution at each time point on the current trial to “predict” the orientation on the previous trial.

This previous-trial decoding is shown for two separate experiments in the figure below. Time zero represents the onset of the sample stimulus on the current trial. In both experiments, we could decode the orientation from the previous trial in the period following the onset of the current-trial sample stimulus (gray regions are statistically significant after controlling for multiple comparisons; chance = 1/16).

These results indicate that a representation of the previous-trial orientation was activated (and therefore decodable) by the onset of the current-trial stimulus. We can’t prove that this reactivation was actually responsible for the behavioral priming effect, but this at least establishes the plausibility of reactivation as a mechanism of priming (as hypothesized many years ago by Gordon Logan).

This study also demonstrates the power of applying decoding methods to ERP data. These methods allow us to track the information that is currently being represented by the brain, and they have amazing sensitivity to quite subtle effects. Frankly, I was quite surprised when Gi-Yeul first showed me that he could decode the orientation of the previous-trial target. And I wouldn’t have believed it if he hadn’t shown that he replicated the result in an independent set of data.

Gi-Yeul has made the data and code available at https://osf.io/dbgh6/. Please take his code and apply it to your own data!

]]>I’ve been thinking about this issue for the last 2 years, as my lab has been working on a new method for quantifying data quality in ERP experiments (stay tuned for a preprint). It turns out that ordinary measures of reliability are quite unsatisfactory for assessing whether ERP data are noisy. This is also true for reaction time (RT) data. A couple days ago, Michaela DeBolt (@MDeBoltC) alerted me to a new paper by Hedge et al. (2018) showing that typical measures of reliability can be low even when power is high in experimental studies. There’s also a recent paper on MRI data quality by Brandmaier et al. (2018) that includes a great discussion of how the term “reliability” is used to mean different things in different fields.

Here’s a quick summary of the main issue: Psychologists usually quantify reliability using correlation-based measures such as Cronbach’s alpha. Because the magnitude of a correlation depends on the amount of true variability among participants, these measures of reliability can go up or down a lot depending on how homogeneous the population is. All else being equal, a correlation will be lower if the participants are more homogeneous. Thus, reliability (as typically quantified by psychologists) depends on the range of values in the population being tested as well as the nature of the measure. That’s like a physicist saying that the reliability of a thermometer depends on whether it is being used in Chicago (where summers are hot and winters are cold) or in San Diego (where the temperature hovers around 72°F all year long).

One might argue that this is not really what psychometricians mean when they’re talking about reliability (see Li, 2003, who effectively redefines the term “reliability” to capture what I will be calling “precision”). However, the way I will use the term “reliability” captures the way this term has been operationalized in 100% of the papers I have read that have quantified reliability (and in the classic texts on psychometrics cited by Li, 2003).

Let’s look at this in the context of a simple reaction time experiment. Imagine that two researchers, Dr. Careful and Dr. Sloppy use exactly the same task to measure mean RT (averaged over 50 trials) from each person in a sample of 100 participants (drawn from the same population). However, Dr. Careful is meticulous about reducing sources of extraneous variability, and every participant is tested by an experienced research assistant at the same time of day (after a good night’s sleep) and at the same time since their last meal. In contrast, Dr. Sloppy doesn’t worry about these sources of variance, and the participants are tested by different research assistants at different times of day, with no effort to control sleepiness or hunger. The measures should be more reliable for Dr. Careful than for Dr. Sloppy, right? Wrong! Reliability (as typically measured by psychologists) will actually be higher for Dr. Sloppy than for Dr. Careful (assuming that Dr. Sloppy hasn’t also increased the trial-to-trial variability of RT).

To understand why this is true, let’s take a look at how reliability would typically be measured in a study like this. One common way to quantify the reliability of the RT measure is the split-half reliability. (There are better measures of reliability for this situation, but they all lead to the same problem, and split-half reliability is easy to explain.) To compute the split-half reliability, the researchers divide the trials for each participant into odd-numbered and even-numbered trials, and they calculate the mean RT separately for the odd- and even-numbered trials. This gives them two values for each participant, and they simply compute the correlation between these two values. The logic is that, if the measure is reliable, then the mean RT for the odd-numbered trials should be pretty similar to the mean RT for the even-numbered trials in a given participant, so individuals with a fast mean RT for the odd-numbered trials should also have a fast mean RT for the even-numbered trials, leading to a high correlation. If the measure is unreliable, however, the mean RTs for the odd- and even-numbered trials will often be quite different for a given participant, leading to a low correlation.

However, correlations are also impacted by the range of scores, and the correlation between the mean RT for the odd- versus even-numbered trials will end up being greater for Dr. Sloppy than for Dr. Careful because the range of mean RTs is greater for Dr. Sloppy (e.g., because some of Dr. Sloppy’s participants are sleepy and others are not). This is illustrated in the scatterplots below, which show simulations of the two experiments. The experiments are identical in terms of the precision of the mean RT measure (i.e., the trial-to-trial variability in RT for a given participant). The only thing that differs between the two simulations is the range of true mean RTs (i.e., the mean RT that a given participant would have if there were no trial-by-trial variation in RT). Because all of Dr. Careful’s participants have mean RTs that cluster closely around 500 ms, the correlation between the mean RTs for the odd- and even-numbered trials is not very high (r=.587). By contrast, because some of Dr. Sloppy’s participants are fast and others are slow, the correlation is quite good (r=.969). Thus, simply by allowing the testing conditions to vary more across participants, Dr. Sloppy can report a higher level of reliability than Dr. Careful.

Keep in mind that Dr. Careful and Dr. Sloppy are measuring mean RT in exactly the same way. The actual measure is identical in their studies, and yet the measured reliability differs dramatically across the studies because of the differences in the range of scores. Worse yet, the sloppy researcher ends up being able to report higher reliability than the careful researcher.

Let’s consider an even more extreme example, in which the population is so homogeneous that every participant would have the same mean RT if we averaged together enough trials, and any differences across participants in observed mean RT are entirely a result of random variation in single-trial RTs. In this situation, the split-half reliability would have an expected value of zero. Does this mean that mean RT is no longer a valid measure of processing speed? Of course not—our measure of processing speed is exactly the same in this extreme case as in the studies of Dr. Careful and Dr. Sloppy. Thus, a measure can be valid even if it is completely unreliable (as typically quantified by psychologists).

Here’s another instructive example. Imagine that Dr. Careful does two studies, one with a population of college students at an elite university (who are relatively homogeneous in age, education, SES, etc.) and one with a nationally representative population of U.S. adults (who vary considerably in age, education, SES, etc.). The range of mean RT values will be much greater in the nationally representative population than in the college student population. Consequently, even if Dr. Careful runs the study in exactly the same way in both populations, the reliability will likely be much greater in the nationally representative population than in the college student population. Thus, reliability (as typically measured by psychologists) depends on the range of scores in the population being measured and not just on the properties of the measure itself. This is like saying that a thermometer is more reliable in Chicago than in San Diego simply because the range of temperatures is greater in Chicago.

Now let’s imagine that Dr. Careful and Dr. Sloppy don’t just measure mean RT in a single condition, but they instead test the effects of a within-subjects experimental manipulation. Let’s make this concrete by imagining that they conduct a flankers experiment, in which participants report whether a central arrow points left or right while ignoring flanking stimuli that are either compatible or incompatible with the central stimulus (see figure). In a typical study, mean RT would be slowed on the incompatible trials relative to the compatible trials (a compatibility effect).

If we look at the mean RTs in a given condition of this experiment, we will see that the mean RT varies from participant to participant much more in Dr. Sloppy’s version of the experiment than in Dr. Careful’s version (because there is more variation in factors like sleepiness in Dr. Sloppy’s version). Thus, as in our original example, the split-half reliability of the mean RT for a given condition will again be higher for Dr. Sloppy than for Dr. Careful. But what about the split-half reliability of the flanker compatibility effect? We can quantify the compatibility effect as the difference in mean RT between the compatible and incompatible trials for a given participant, averaged across left-response and right-response trials. (Yes, there are better ways to analyze these data, but they all lead to the same conclusions about reliability.) We can compute the split-half reliability of the compatibility effect by computing it twice for every subject—once for the odd-numbered trials and once for the even-numbered trials—and calculating the correlation between these values.

The compatibility effect, like the raw RT, is likely to vary according to factors like the time of day, so the range of compatibility effects will be greater for Dr. Sloppy than for Dr. Careful. And this means that the split-half reliability will again be greater for Dr. Sloppy than for Dr. Careful. (Here I am assuming that trial-to-trial variability in RT is not impacted by the compatibility manipulation and by the time of day, which might not be true, but nonetheless it is likely that the reliability will be at least as high for Dr. Sloppy as for Dr. Careful.)

By contrast, statistical power for determining whether a compatibility effect is present will be greater for Dr. Careful than for Dr. Sloppy. In other words, if we use a one-sample t test to compare the mean compatibility effect against zero, the greater variability of this effect in Dr. Sloppy’s experiment will reduce the power to determine whether a compatibility effect is present. So, even though reliability is greater for Dr. Sloppy than for Dr. Careful, statistical power for detecting an experimental effect is greater for Dr. Careful than for Dr. Sloppy. If you care about statistical power for experimental effects, reliability is probably not the best way for you to quantify data quality.

What if Dr. Careful and Dr. Sloppy wanted to look at individual differences? For example, imagine that they were testing the hypothesis that the flanker compatibility effect is related to working memory capacity. Let’s assume that they measure both variables in a single session. Assuming that both working memory capacity and the compatibility effect vary as a function of factors like time of day, Dr. Sloppy will find greater reliability for both working memory capacity and the compatibility effect (because the range of values is greater for both variables in Dr. Sloppy’s study than in Dr. Careful’s study). Moreover, the correlation between working memory capacity and the compatibility effect will be higher in Dr. Sloppy’s study than in Dr. Careful’s study (again because of differences in the range of scores).

In this case, greater reliability is associated with stronger correlations, just as the psychometricians have always told us. All else being equal, the researcher who has greater reliability for the individual measures (Dr. Sloppy in this example) will find a greater correlation between them. So, if you want to look at correlations between measures, you want to maximize the range of scores (which will in turn maximize your reliability). However, recall that Dr. Careful had more statistical power than Dr. Sloppy for detecting the compatibility effect. Thus, the same factors that increase reliability and correlations between measures can end up reducing statistical power when you are examining experimental effects with exactly the same measures. (Also, if you want to look at correlations between RT and other measures, I recommend that you read Miller & Ulrich, 2013, which shows that these correlations are more difficult to interpret than you might think.)

It’s also important to note that Dr. Sloppy would run into trouble if we looked at test-retest reliability instead of split-half reliability. That is, imagine that Dr. Sloppy and Dr. Careful run studies in which each participant is tested on two different days. Dr. Careful makes sure that all of the testing conditions (e.g., time of day) are the same for every participant, but Dr. Sloppy isn’t careful to keep the testing conditions constant between the two session for each participant. The test-retest reliability (the correlation between the measure on Day 1 and Day 2) would be low for Dr. Sloppy. Interestingly, Dr. Sloppy would have high split-half reliability (because of the broad range of scores) but poor test-retest reliability. Dr. Sloppy would also have trouble if the compatibility effect and working memory capacity were measured on different days.

Now let’s turn to the distinction between reliability and precision. The first part of the Brandmaier et al. (2018) paper has an excellent discussion of how the term “reliability” is used differently across fields. In general, everyone agrees that a measure is reliable to the extent that you get the same thing every time you measure it. The difference across fields lies in how reliability is quantified. When we think about reliability in this way, a simple way to quantify it would be to obtain the measure a large number of times under identical conditions and compute the standard deviation (SD) of the measurements. The SD is a completely straightforward measure of the “the extent that you get the same thing every time you measure it.” For example, you could use a balance to weigh an object 100 times, and the standard deviation of the weights would indicate the reliability of the balance. Another term for this would be the “precision” of the balance, and I will use the term “precision” to refer to the SD over multiple measurements. (In physics, the SD is typically divided by the mean to get the coefficient of variability, which is often a better way to quantify reliability for measures like weight that are on a ratio scale.)

The figure below (from the Brandmaier article) shows what is meant by low and high precision in this context, and you can see how the SD would be a good measure of precision. The key is that precision reflects the variability of the measure around its mean, not whether the mean is the true mean (which would be the accuracy or bias of the measure).

From Brandmaier et al. (2018)

Things are more complicated in most psychology experiments, where there are (at least) two distinct sources of variability in a given experiment: true differences among participants (called the true score variance) and measurement imprecision. However, in a typical experiment, it is not obvious how to separately quantify the true score variance from the measurement imprecision. For example, if you measure a dependent variable once from N participants, and you look at the variance of those values, the result will be the sum of the true score variance and the variance due to measurement error. These two sources of variance are mixed together, and you don’t know how much of the variance is a result of measurement imprecision.

Imagine, however, that you’ve measured the dependent variable twice from each subject. Now you could ask how close the two measures are to each other. For example, if we take our original simple RT experiment, we could get the mean RT from the odd-number trials and the mean RT from the even-numbered trials in each participant. If these two scores were very close to each other in each participant, then we would say we have a precise measure of mean RT. For example, if we collected 2000 trials from each participant, resulting in 1000 odd-numbered trials and 1000 even-numbered trials, we’d probably find that the two mean RTs for a given subject were almost always within 10 ms of each other. However, if collected only 20 trials from each participant, we would see big differences between the mean RTs from the odd- and even-numbered trials. This makes sense: All else being equal, mean RT should be a more precise measure if it’s based on more trials.

In a general sense, we’d like to say that mean RT is a more reliable measure when it’s based on more trials. However, as the first part of this blog post demonstrated, typical psychometric approaches to quantifying reliability are also impacted by the range of values in the population and not just the precision of the measure itself: Dr. Sloppy and Dr. Careful were measuring mean RT with equal precision, but split-half reliability was greater for Dr. Sloppy than for Dr. Careful because there was a greater range of mean RT values in Dr. Sloppy’s study. This is because split-half reliability does not look directly at how similar the mean RTs are for the odd- and even-numbered trials; instead, it involves computing the correlation between these values, which in turn depends on the range of values across participants.

How, then, can we formally quantify precision in a way that does not depend on the range of values across participants? If we simply took the difference in mean RT between the odd- and even-numbered trials, this score would be positive for some participants and negative for others. As a result, we can’t just average this difference across participants. We could take the absolute value of the difference for each participant and then average across participants, but absolute values are problematic in other ways. Instead, we could just take the standard deviation (SD) of the two scores for each person. For example, if Participant #1 had a mean RT of 515 ms for the odd-numbered trials and a mean RT of 525 ms for the even-numbered trials, the SD for this participant would be 7.07 ms. SD values are always positive, so we could average the single-participant SD values across participants, and this would give us an aggregate measure of the precision of our RT measure.

The average of the single-participant SDs would be a pretty good measure of precision, but it would underestimate the actual precision of our mean RT measure. Ultimately, we’re interested in the precision of the mean RT for all of the trials, not the mean RT separately for the odd- and even-numbered trials. By cutting the number of trials in half to get separate mean RTs for the odd- and even-numbered trials, we get an artificially low estimate of precision.

Fortunately, there is a very familiar statistic that allows you to quantify the precision of the mean RT using all of the trials instead of dividing them into two halves. Specifically, you can simply take all of the single-trial RTs for a given participant in a given condition and compute the standard error of the mean (SEM). This SEM tells you what you would expect to find if you computed the mean RT for that subject in each of an infinite number of sessions and then took the SD of the mean RT values.

Let’s unpack that. Imagine that you brought a single participant to the lab 1000 times, and each time you ran 50 trials and took the mean RT of those 50 trials. (We’re imagining that the subject’s performance doesn’t change over repeated sessions; that’s not realistic, of course, but this is a thought experiment so it’s OK.) Now you have 1000 mean RTs (each based on the average of 50 trials). You could take the SD of those 1000 mean RTs, and that would be an accurate way of quantifying the precision of the mean RT measure. It would be just like a chemist who weighs a given object 1000 times on a balance and then uses the SD of these 1000 measurements to quantify the precision of the balance.

But you don’t actually need to bring the participant to the lab 1000 times to estimate the SD. If you compute the SEM of the 50 single-trial RTs in one session, this is actually an estimate of what would happen if you measured mean RT in an infinite number of sessions and then computed the SD of the mean RTs. In other words, the SEM of the single-trial RTs in one session is an estimate of the SD of the mean RT across an infinite number of sessions. (Technical note: It would be necessary to deal with the autocorrelation of RT across trials, but there are methods for that.)

Thus, you can use the SEM of the single-trial RTs in a given session as a measure of the precision of the mean RT measure for that session. This gives you a measure of the precision for each individual participant, and you can then just average these values across participants. Unlike traditional measures of reliability, this measure of precision is completely independent of the range of values across the population. If Dr. Careful and Dr. Sloppy used this measure of precision, they would get exactly the same value (because they’re using exactly the same procedure to measure mean RT in a given participant). Moreover, this measure of precision is directly related to the statistical power for detecting differences between conditions (although there is a trick for aggregating the SEM values across participants, as will be detailed in our paper on ERP data quality).

So, if you want to assess the quality of your data in an experimental study, you should compute the SEM of the single-trial values for each subject, not some traditional measure of “reliability.” Reliability is very important for correlational studies, but it’s not the right measure of data quality in experimental studies.

Here’s the bottom line: the idea that “a measure cannot be valid if it is not reliable” is not true for experimentalists (given how reliability is typically operationalized by psychologists), and they should focus on precision rather than reliability.

]]>Why do rats and monkeys press levers in experiments on reinforcement learning? Because pressing the lever produces food or water, obviously. That’s a fundamental part of how most psychologists and neuroscientists think about reinforcement learning.

If people or animals could get money/food without working for it, they would never work. In other words, everyone would be a freeloader given the chance. Right?

Wrong. Studies going back to 1963 show that animals will push buttons and press levers to get food even if they have easy access to a container of equivalent food. What? Given the opportunity to freeload, animals will still work? That’s crazy! But it’s true. Humans will also work for candy or coins in the presence of free candy or coins. This is called “contra-freeloading” because it’s the opposite of freeloading.

Allen Neuringer

I first heard about contra-freeloading from one of my undergrad mentors at Reed College, Allen Neuringer, who published one of the first papers on it in Science in 1969. The title of the paper beautifully captures the central finding: “Animals respond for food in the presence of free food.” This provocative paper—published in one of the most widely read scientific journals—has been cited by other researchers fewer than 300 times in the 50 years since it was published. Responding for food in the presence of free food has since been observed in species ranging from pigeons and rats to giraffes, parrots, and monkeys, but most psychologists and neuroscientists are completely unaware of this phenomenon. (Interestingly, cats appear to be an exception; they will work for food only if there is no other choice. Cats are nature’s freeloaders.)

One theory is that contra-freeloading occurs because it helps organisms gain information about the environment that might be useful later. If you know that pressing a lever gets you food, this might come in handy if other sources of food disappear. This does not seem like a very compelling explanation, however, because (under some conditions) animals will respond at a very high rate to get food in the presence of free food. It’s not like they’re just checking to see if the lever still works from time to time. (See also this elegant study showing that monkeys will work to get information about the size of the next reinforcer, even though this has no impact on whether they will get the reinforcer and gives them no long-term information.)

Contra-freeloading seems like an important phenomenon for economists and policymakers: People don’t just work for money, and they are not inevitably freeloaders. Sure, people will often freeload when given the chance. But the factors that motivate human behavior are far more complex than a simple desire to maximize income.

Contra-freeloading is also important for psychologists and neuroscientists: Organisms are not motivated solely by gaining rewards and avoiding punishments. If we want to understand the neural mechanisms underlying behavior, we cannot simply focus on explicit rewards and punishments.

I occasionally hear psychologists and especially behavioral neuroscientists say something along the lines of: “All learned behavior is controlled by reinforcement. The reinforcer may be nonobvious, but it’s there. After all, why else would an organism do something?” But this is a completely circular argument: “We see that an organism is pressing a lever, so it must be getting some kind of reinforcer.” (For experts: the Premack principle can sometimes be used to avoid this circularity, but it does not explain why an animal would respond for food in the presence of free food.)

An economist might try a parallel move, saying that people try to maximize “utility” and not just income (where “utility” is essentially “whatever someone thinks is valuable”). But this is also a circular argument: “We see that people are working, so they must be getting something of value for their work.” In other words, when people work without getting paid, we assume that they must be getting something else they find valuable (some kind of utility). But this is usually just an assumption and is typically unfalsifiable. Does this assumption really add anything to our explanation of human behavior, or is it just a soup stone?

To understand contra-freeloading, we need to make a distinction between “responding because of reinforcement” and “responding to obtain the reinforcer.” When pressing a lever produces food, a rat will press the lever. Rats don’t press levers just because they enjoy lever pressing (just as I don’t go to work because I enjoy spending my days answering endless emails). If the lever stops producing food, the rat will stop pressing the lever. Allen Neuringer’s 1969 article showed that rats and pigeons will respond *for food *in the presence of free food, but they will stop responding if they stop getting food for their responses. Curiously, they are responding *because the lever produces food*, but not *because they need the food*. It’s as if they are responding so that they can have the experience of producing food, not just to get the food itself.

By analogy, most people would probably quit their jobs if they stopped getting paid, but this does not mean that people work solely to get paid. First, they need the paycheck—they’re not like rats who are responding for food in the presence of free food. A more analogous situation would be people who keep working after they win the lottery. Or retirees with good pensions who go back to work even though they don’t really need the money. We can attempt to explain unpaid work by saying that people must be trying to obtain some other kind of reinforcer, but this is circular and doesn’t actually explain anything.

The idea that money and other overt reinforcers are the best way to motivate human behavior can have some unpleasant consequences. When CEOs are given strong financial incentives to maximize share prices, this incentivizes them to inflate short-term share prices rather than working to maximize long-term value. When scientists are given promotions and salary increases when they publish papers in prestigious journals, this incentivizes them to engage in p-hacking and other questionable research practices.

But this doesn’t mean we can ignore incentives. Although rats will press a lever to get food in the presence of free food, they will stop pressing the lever if it stops producing food. That seems completely counterintuitive: If the rats don’t need the food, why do they press the lever only if it produces food?

Motivation is both vexingly and wonderfully complicated!

]]>Since the classic study of Worden et al. (2000), we have known directing attention to the location of an upcoming target leads to a suppression of alpha-band EEG activity over the contralateral hemisphere. This is usually thought to reflect a preparatory process that increases cortical excitability in the hemisphere that will eventually process the upcoming target (or decreases excitability in the opposite hemisphere). This can be contrasted with the N2pc component, which reflects the focusing of attention onto a currently visible target (reviewed by Luck, 2012). But do these different neural signals actually reflect similar underlying attentional mechanisms? The answer in a new study by Felix Bacigalupo (now on the faculty at Pontificia Universidad Catolica de Chile) appears to be both “yes” (the N2pc component and lateralized alpha suppression can both be triggered by a target, and they are both influenced by some of the same experimental manipulations) and “no” (they have different time courses and are influenced differently by other manipulations).

The study involved two experiments that we were designed to determine whether (a) lateralized alpha suppression would be triggered by a target in a visual search array, and (b) whether this effect could be experimentally dissociated from the N2pc component. The first experiment (shown in the figure below) used a fairly typical N2pc design. Subjects searched for an item of a specific color for a given block of trials. The target color appeared (unpredictably) at one of four locations. Previous research has shown that the N2pc component is primarily present for targets in the lower visual field, and we replicated this result (see ERP waveforms below). We also found that, although alpha-band activity was suppressed over both hemispheres following target presentation, this suppression was greater over the hemisphere contralateral to the target. Remarkably, like the N2pc component, the target-elicited lateralized alpha suppression (TELAS) occurred primarily for targets in the lower visual field. However, the time course of the TELAS was quite different from that of the N2pc. The scalp distribution of the TELAS also appeared to be more posterior than that of the N2pc component (although this was not formally compared).

The second experiment included a crowding manipulation, following up on a previous study in which the N2pc component was found to be largest when flanked by distractors that are at the edge of the crowding range, with a smaller N2pc when the distractors are so close that they prevent perception of the target shape (Bacigalupo & Luck, 2015). We replicated the previous result, but we saw a different pattern with the lateralized alpha suppression: The TELAS effect tended to increase progressively as the flanker distance decreased, with the largest magnitude for the most crowded displays. Thus, the TELAS effect appears to be related to difficulty or effort, whereas the N2pc component appears to be related to whether or not the target is successfully selected.

The bottom line is that visual search targets trigger both an N2pc component and a contralateral suppression of alpha-band EEG oscillations, especially when the targets are in the lower visual field, but the N2pc component and the TELAS effect can also be dissociated, reflecting different mechanisms of attention.

These results are also relevant for the question of whether lateralized alpha effects reflect an increase in alpha in the nontarget hemisphere to suppress information that would otherwise be processed by that hemisphere or, instead, a decrease in alpha in the target hemisphere to enhance the processing of target information. If the TELAS effect reflected processes related to distractors in the hemifield opposite to the target, then we would not expect it to be related to whether the target was in the upper or lower field or whether flankers were near the target item. Thus, the present results are consistent with a role of alpha suppression in increasing the processing of information from the target itself (see also a recent review paper by Josh Foster and Ed Awh).

One interesting side finding: The contralateral positivity that often follows the N2pc component (similar to a Pd component) was clearly present for the upper-field targets. It was difficult to know the amplitude of this component for the lower-field targets given the overlapping N2pc and SPCN components, but the upper-field targets clearly elicited a strong contralateral positivity with little or no N2pc. This provides an interesting dissociation between the post-N2pc contralateral positivity and the N2pc component.

]]>This is our second paper applying decoding methods to sustained ERPs and alpha-band EEG oscillations. The first one decoded which of 16 orientations was being maintained in working memory. In the new paper, we decoded which of 16 directions of motion was present in random dot kinematograms.

The paradigm is shown in the figure below. During a 1500-ms motion period, 25.6% or 51.2% of the dots moved coherently in one of 16 directions and the remainder moved randomly. After the motion ended, the subject adjusted a green line to match the direction of motion (which they could do quite precisely).

We asked whether we could decode (using machine learning) the precise direction of motion from the scalp distribution of the sustained voltage or alpha-band signal at each moment in time. Decoding the exact direction of motion is very challenging, and chance performance would be only 6.25% correct. During the motion period for the 51.2% coherence level, we were able to decode the direction of motion well above chance on the basis of the sustained ERP voltage (see the bottom right panel of the figure). However, as shown in the bottom left panel, we couldn’t decode the direction of motion on the basis of the alpha-band activity until the report period (during which time attention was presumably focused on the location of the green line).

When the coherence level was only 25.6% (and perception of coherent motion was much more difficult), we could not decode the actual direction of motion above chance. However, we were able to decode the direction of perceived motion (i.e., the direction that the subject reported at the end of the trial).

This study shows that (a) ERPs can be used to decode very subtle stimulus properties, and (b) sustained ERPs and alpha-band oscillations contain different information. In general, alpha-band activity appears to reflect the direction of spatial attention, whereas sustained ERPs contain information about both the direction of attention and the specific feature value being represented.

]]>[Note: Our experience is in Psychology and Neuroscience, but this probably applies to most other disciplines.]

It is now the season for students in the U.S. to begin the stressful, arduous, and sometimes expensive process of applying to PhD programs. One common piece of advice (that we give our own students) is to send emails to faculty at the institutions where you plan to apply. In this blog post, we explain why this is a good thing to do and how to do it. Some students find it very stressful to send these emails, and we hope that the “how to do it” section will make it less stressful. You don’t have to email the faculty, but it can be extremely helpful, and we strongly recommend that you do it.

In many programs (especially in Psychology), individual faculty play a huge role in determining which students are accepted into the PhD program. In these programs, students are essentially accepted into the lab of a specific faculty member, and the faculty are looking for students who have the knowledge, skills, and interests to succeed in their labs. This is often called the “apprenticeship model.”

In other programs (including most Neuroscience programs), admissions decisions are made by a committee, and individual faculty mentors play less of a role. Moreover, in most Neuroscience programs, grad students do lab rotations in the first year and do not commit to a specific lab until the second year. We’ll call this the “committee model.”

Although many students are accepted into graduate programs without emailing faculty prior to submitting applications to programs, there are many good reasons to do so. This can be especially useful for programs that use the apprenticeship model. First, you can find out whether they are actually planning to take new students. You don't want to waste money applying to a given program only to find out that the one faculty member of interest isn’t taking students this year (or is about to move to another university, take a job in industry, etc.). Information about this may be on the program’s web site or the faculty member’s web site, but web sites are often out of date, so it’s worth double-checking with an email.

Second, and perhaps most important, this email will get you “on the radar” of the faculty. Most PhD programs get hundreds of applicants, and faculty are much more likely to take a close look at your application if you’ve contacted them in advance.

Third, you might get other kinds of useful information. For example, a professor might write back saying something like “I’m not taking any new students, but we’ve just hired a new faculty member in the same area, and you might consider working with her.” Or, the professor might say something like “When you apply, make sure that you check the XXX box, which will make you eligible for a fellowship that is specifically for people from your background.” Or, if the professor accepts students through multiple programs (e.g., Psychology and Neuroscience), you might get information about which one to apply to or whether to apply to both programs. Both of us take students from multiple different graduate programs, and we often provide advice about which program is best for a given student (which can impact the likelihood of being accepted as well as the kinds of experiences the students will get).

If admissions are being done by a committee, an email can still be important. For example, decisions may take into account whether the most likely mentor(s) are interested in the student. Or you might find out that none of the faculty of interest in a given program are currently taking students for lab rotations. This could impact the likelihood that you get into a program, and it might make you less interested in a program if you know in advance that you won’t have the opportunity to do a rotation in that person’s lab. In addition, faculty members can (and will) contact the committee before decisions are made to ask them to take a close look at a particular student’s application, pointing out things that might not otherwise be obvious to them. Finally, the faculty are often involved in the interview process, and having already established a relationship will make the interview less intimidating and more productive.

Now that you are (we hope) convinced that you should contact the faculty, you have to muster up the courage to actually send that message, and you need to make sure that your message is effective. To address both of these issues, we’ll provide give you some general advice and then provide an email template that you can use as a starting point.

First, the general advice. Faculty are very busy, and they get a lot of emails that aren’t worth reading. Each of us gets many emails each year from prospective students, and we find that the right e-mail can pique our interest and make us look carefully at a student’s materials. On the other hand, generic e-mails that simply say “Are you accepting students” are likely to be ignored.

You need to make sure that your email is brief but has some key information to get their interest. We recommend a subject heading such as “Inquiry from potential graduate applicant.” For the main body of the email, your goals are to (a) introduce yourself, (b) inquire about whether they are taking students, (c) make it clear why you are interested in that particular faculty member, and (d) get any advice they might offer. Here’s an example:

Dear Dr. XXX,

I’m in my final year as a Cognitive Science major at XXXX, where I have been working in the lab of Dr. XXX XXX. My research has focused on attention and working memory using psychophysical and electrophysiological methods (see attached CV). I’m planning to apply to PhD programs this Fall, and I’m very interested in the possibility of working in your lab at UC Davis. I read your recent paper on XXX, and I found your approach to be very exciting.

I was hoping you might tell me whether you are planning to take new students in your lab in Fall 2019 [or: …whether you are planning to take rotation students in your lab…]. I’d also be interested in any other information or advice you have.

[Possibly add a few more lines here about your background and interests.]

Sincerely,

XXX XXXX

It’s useful to include some details about yourself—where you got or are getting your degree, what kind of research experience you’ve had, and/or what you’ve been doing since you graduated. Even if your research experience isn’t directly related to what you want to do, it’s a good idea to include at least a phrase about what you’ve been doing (e.g., “I did internships in a neuroscience lab working with rodents and a social psychology lab administering questionnaires”). But if this experience is very different from the intended mentor’s research, you need to make it clear that you’re planning to move in a different direction for your graduate work. We also pay more attention to emails from students who seem to know something about us. Mention a paper or a research project you saw on the professor’s website. You don’t need details; just show that you’ve done your homework and are truly interested in that individual.

It’s a good idea to attach a CV, even though there won’t be a lot on it. That’s a good place to provide some more details about your skills and experience. Also, if you have an excellent GPA or outstanding GRE scores, you can put them on your CV (although these would not go on a CV for most other purposes). Your goal is to stand out from the crowd, so you should include anything relevant that will be impressive (e.g., “3 years of intensive Python programming experience” but not “Familiarity with Excel and PowerPoint”). Don’t put posters, papers in progress, etc., in a section labeled “Publications” – that section should be reserved for papers/chapters that have actually been accepted for publication. You should include these things, but use more precise labels like “Manuscripts in Progress”, “Conference Presentations”, etc.

If you’re a member of an underrepresented/disadvantaged group, you can make this clear in your email or CV if you are comfortable doing so (although this may depend on your field). We recognize that this can sometimes be a sensitive issue, but there are often special funding opportunities for students with particular underrepresented identities, and most faculty are especially eager to recruit students from underrepresented/disadvantaged groups. Usually, this information can be provided indirectly (e.g., by listing scholarships you’ve received or programs that you’ve participated in, such as the McNair Scholars), but it can be helpful if you make this information explicit to your prospective faculty mentor and program. However, this can backfire if it’s not done just right, so we strongly recommend that you ask your current faculty mentor for advice about the best way to do this given your field and your specific situation.

No matter what your situation, we recommend having your faculty mentor(s) take a look at a draft of the email and your CV before you send them. Grad students and postdocs can also be helpful, but they may not really know what is appropriate given that they haven’t been on the receiving end of these emails.

Most importantly, don’t be afraid to send the email. The worst thing that will happen is that the faculty member doesn’t read it and doesn’t remember that you ever sent it. The best thing that can happen is that the e-mail leads to a conversation that helps you get accepted into the program of your dreams.

Many faculty will simply not reply. In this case, no information is no information. There are many faculty who simply don’t read this kind of e-mail, and a “no reply” might mean you contacted one of those faculty. Of course, it’s also possible that they’re not interested in taking grad students and didn’t want to spend time replying. Or, it could mean that the message was caught by a spam filter, that they received 150 emails that day, etc. So, if you really want to work with that person, you may still want to apply.

You may get a brief response that says something like “Yes, I’m taking students, and I encourage you to apply” or “I’m always looking for qualified students.” This indicates that the faculty member will likely look at applications, and you don’t need to follow-up.

If you’re lucky, you may get a more detailed response that will lead to a series of email exchanges and perhaps an invitation to chat (usually on Skype or something similar). This will be more likely if you say something about what you’ve done and why you are interested in this lab. We know it may be stressful to actually talk to the faculty member, but isn’t that what you’re hoping to do in graduate school? Now is the time to get over that hurdle.

You may get a response like “I’m not taking new students this year” or “I probably won’t take new students this year” or “I’m not currently taking rotation students” (which is code for “don’t bother applying to work with me”). Or you might get something like “Given your background and interests, I don’t think you’d be a good fit for my lab.” Now you know not to waste your money applying to work with that person, so you’ve learned something valuable.

We’ve never heard of a student receiving a rude or unpleasant response. It may happen, but it would be extremely rare. So, you really don’t have much to lose by emailing faculty, and you have a lot to gain. It’s not 100% necessary, but it will likely increase your odds of getting into one of the programs you most want to attend.

]]>In several behavioral studies using change detection/localization tasks, we have previously shown that people with schizophrenia (PSZ) exhibit large reductions in visual working memory storage capacity (Kmax). In one large study with 99 PSZ and 77 healthy control subjects (HCS), we found an effect size (Cohen's d) of 1.11, and the degree of Kmax reduction statistically accounted for approximately 40% of the reduction in overall cognitive ability exhibited by PSZ (as measured with the MATRICS Battery). Change detection tasks are much simpler than most working memory tasks, focus on storage rather than manipulation, and can be used across species. Thus, Kmax gives us a measure that is both neurobiologically tractable and strongly related to broad cognitive dysfunction.

In our most recent work, led by Dr. Britta Hahn at the Maryland Psychiatric Research Center, we used fMRI to examine the neuroanatomical substrates of reduced Kmax in PSZ. We took advantage of an approach pioneered by Todd and Marois (2004, Nature), in which a whole-brain analysis is used to find clusters of voxels where the BOLD signal is related to the amount of information actually stored in working memory (K). As shown in the figure below, we found the same areas of posterior parietal cortex (PPC) that were observed by Todd and Marois.

In the left PPC, however, the K-dependent modulation of activity was reduced in PSZ relative to HCS. As shown in the scatterplots, the BOLD signal in this region was strongly related to the number of items being held in working memory (K) in HCS, but the function was essentially flat in PSZ. However, the overall level of activation was just as great in PSZ as in HCS (the Y intercept). The reduced slope was driven mainly by an overactivation in PSZ relative to HCS when relatively little information was being stored in memory. Moreover, the slope was strongly correlated with overall cognitive ability (again measured using the MATRICS Battery), and the degree of slope reduction statistically accounted for over 40% of the reduction in broad cognitive ability in PSZ.

One particularly interesting aspect of these results is that they point to posterior parietal cortex as a potential source of cognitive dysfunction in schizophrenia, whereas most research and theory has focused on prefrontal cortex. Studies with healthy young adults have consistently identified PPC as a major player in working memory capacity and in the ability to divide attention, both of which are strongly impaired in PSZ. We hope that our study motivates more research to examine the potential contribution of the PPC to cognitive dysfunction in schizophrenia.

]]>Working memory is often conceived as a buffer that holds information currently being operated upon. However, many studies have shown that it is possible to perform fairly complex tasks (e.g., visual search) that are interposed during the retention interval of a change detection task with minimal interference (especially load-dependent interference). One possible explanation is that the information from the change detection task can be held in some other form (e.g., activity-silent memory) while the interposed task is being performed. If so, this might be expected to have subtle effects on the memory for the stimulus.

To test this, we had subjects perform a delayed estimation task, in which a single teardrop-shaped stimulus was held in memory and was reproduced at the end of the trial (see figure below). A single letter stimulus was presented during the delay period on some trials. We asked whether performing a very simple task with this interposed stimulus would cause a subtle disruption in the memory for the teardrop's orientation. In some trial blocks, subjects simply ignored the interposed letter, and we found that it produced no disruption of the memory for the teardrop. In other trial blocks, subjects had to make a speeded response to the interposed letter, indicating whether it was a C or a D. Although this was a simple task, and only a single object was being maintained in working memory, the interposed stimulus caused the memory of the teardrop to become less precise and more categorical.

Thus, performing even a simple task on an interposed stimulus can disrupt a previously encoding working memory representation. The representation is not destroyed, but becomes less precise and more categorical, perhaps indicating that it had been offloaded into a different form of storage while the interposed task was being performed. Interestingly, we did not find this effect when an auditory interposed task was used, consistent with modality-specific representations.

]]>In this article, we show how ridiculously easy it is to find significant effects in ERP experiments by using the observed data to guide the selection of time windows and electrode sites. We also show that including multiple factors in your ANOVAs can dramatically increase the rate of false positives (Type I errors). We provide some suggestions for methods to avoid inflating the Type I error rate.

This paper was part of a special issue of Psychophysiology on Reproducibility edited by Emily Kappenman and Andreas Keil.

]]>Here’s the problem in a nutshell: if we want to provide a tenure-track faculty position for every new PhD who wants one, the number of available positions would need to increase exponentially with no limit. This is shown in the graph below.

If we assume that a typical faculty member has a couple grad students at any given time, and most of them want jobs in academia, this faculty member will have a student who graduates and wants a faculty position approximately every three years. As a result, we would need to create a new faculty position approximately every three years just to keep up with the students from a single current faculty member. As if this wasn’t bad enough, these recent PhDs will then get their own grad students, who will also need faculty positions. This leads to an exponential growth in the number of positions needed to fill the demand.

For example, if we have 1000 positions in a given field in the year 2018, we will need another 1000 positions in that field by the year 2021 to accommodate the new students who have received their PhDs by that time, leading to a total of 2000 positions to accommodate the demand that year. The faculty in these 2000 positions will have students who will need another 2000 positions by the year 2024, leading to a total need for 4000 positions that year.

If the number of positions kept increasing over time to fill the demand, we would need over a million positions by the year 2048! This doesn’t account for retirements, etc., but those factors have a very small effect (unless we start forcing faculty to retire when they reach the age of 40 or some such thing). There are various other assumptions here (e.g., a new PhD every 3 years), but virtually any realistic set of parameters will lead to an exponential or nearly-exponential growth function.

This is just like the exponential increase you might see in the size of a population of organisms, with a rate factor (r) that describes the rate of reproduction. However, an exponential increase can happen only if reproduction is not capped by resource limitations. Resource limitations lead to a maximum population size, which population biologists call K (for the “carrying capacity” of the environment). When the exponential growth with rate r is combined with carrying capacity K, you get a logistic function. This is shown in the picture below (from Khan Academy), which illustrates the growth rate of a population of organisms with no limit on the population size (the exponential function on the left) and with a limit at K (the logistic function on the right).

At early time points, the two functions are very similar: K doesn’t have much impact on the rate of growth in the logistic function early in time, and growth is mainly limited by r (the replication rate). This is called “r-limited” growth. However, later in time, the resource limitations start impacting the rate of growth in the logistic function, and the population size asymptotes at K. This is called “K-limited” growth. It’s much nicer to live in a period of r-limited growth, when there are plenty of resources. When growth is K-limited, this means that the organisms in the population have so few resources that they die before they can reproduce, or are so hungry they can’t reproduce, or their offspring are so hungry they can’t survive, etc. Not a very pleasant life.

In academia, r-limited growth means that jobs are plentiful, and the main limitations on growth are the number of students per lab and the rate at which they complete their degrees. By contrast, K-limited growth basically means that a faculty member needs to die or retire before a new PhD can get a position, and only a small fraction of new PhDs will ever get tenure-track jobs and start producing their own students. This also means that the competition for tenure-track jobs and research grants will be fierce. Sound familiar?

In the context of academia, K represents the maximum number of faculty positions that can be supported by the society. The maximum number of faculty positions might increase gradually over time, as the overall population size increases or as a society becomes wealthier. However, there is no way we can sustain an exponential growth forever (especially if that means we need over a million positions by 2048 in a field that has only a thousand positions in 2018).

I think it’s pretty clear that we’re now in a K-limited period, where the number of positions is increasing far too slowly to keep up with the demand for positions from people getting PhDs. When I was on the job market in the early 1990s, there were already more people with PhDs than available faculty positions. However, the problem of an oversupply of PhDs was partially masked by an increase in the availability of postdoc positions. Also, it was becoming more common for faculty at “second-tier” universities to conduct and publish research, so the actual number of positions that combined research and teaching was increasing. But this balloon has stretched about as far as it can, and highly qualified young scholars are now having trouble getting the kind of position they are seeking (and we’re seeing 200+ applicants for a single position in our department).

In addition to a limited number of tenure-track faculty positions, we have a limited amount of grant money. In some departments and subfields, getting a major grant is required for getting tenure. Even if this isn’t a formal requirement, the resources provided by a grant (e.g., funding for grad students and postdocs) may be essential for an assistant professor to be sufficiently productive to receive tenure. But an increase in grant funding without a commensurate increase in permanent positions can actually make things worse rather than better. We saw that when the NIH budget was doubled between 1994 and 2003. This led to an increase in funding for grad students and postdocs (leading to the balloon I mentioned earlier). However, without an increase in the number of tenure-track faculty positions, there was nowhere for these people to go when they finished their training. Their CVs were more impressive, but this just increased the expectations of search committees. Also, a lot of the increased NIH funding was absorbed by senior faculty (like me) who now had 2, 3, or even 4 grants instead of just 1. As usual, the rich got richer.

One might argue that competition is good, because it means that only the very best people get tenure-track positions and grants. And I would be the first person to agree that competition can help inspire people to be as creative and productive as possible. However, the current state of hypercompetition clearly has a dark side. Some people write tons of grants, often with little thought, in the hopes of getting lucky. This can lead to poorly-conceived projects, and it can leave people with little time to think about and actually conduct high-quality research. And it can lead to p-hacking and other questionable research practices, or even outright fraud. I think we’re way beyond the point at which the level of competition is beneficial.

Now let’s talk about solutions. Should we increase the number of tenure-track faculty positions at research universities? I would argue that any solution of this nature is doomed to failure in the long run. Increasing the number of position is an increase in K, and this just postpones the point at which the job market becomes saturated. It would certainly help the people who are seeking a position now, but the problem will come back eventually. There just isn’t a way for the number of positions to increase exponentially forever.

We could also try to limit the number of students we accept into PhD programs. This would be equivalent to decreasing r, the rate of “reproduction.” However, for this to fully solve the problem, we would need the “birth rate” (number of new PhDs per year in a field) to equal the “death rate” (the number of retirements per year in the field). Here’s another way to look at it: if the number of positions in a field remains constant, a given faculty member can expect to place only a single student in a tenure-track position over the course of the faculty member’s entire career. Is it realistic to restrict the number of PhD students so that faculty can have only one student per career? Or even one per decade? Probably not.

I have only one realistic idea for a solution, which is to create more good positions for PhDs that don’t involve “reproduction” (i.e., training PhD students). For example, if there were good positions outside of academia for a large number of PhDs, this would reduce the demand for tenure-track positions and decrease r, the rate of reproduction (assuming that there would be fewer people “spawning” new students as a result). Tenure-track positions at teaching-oriented institutions have the same effect (as long as these institutions don’t decide to start granting PhDs). I don’t think it’s realistic to increase the number of these teaching-oriented positions (except insofar as they increase with overall changes in population size). However, in many areas of the mind and brain sciences, it appears that the availability of industry positions could increase substantially. Indeed, we are already seeing many of our students and postdocs take jobs at places like Google and Netflix.

Many faculty in research-oriented universities think that success in graduate school means getting a tenure-track faculty position in a research-oriented university. However, if I’m right that the current K-limited growth curve—and the associated hypercompetition—is a major problem, then we should place a much higher value on industry and teaching positions. The availability of these positions will mean that we can continue to have lots of bright graduate students in our labs without dooming them to work as Uber drivers after they get their PhDs. And teaching positions are intrinsically valuable: A great teacher can have a tremendous positive impact on thousands of students over the course of a career.

This doesn’t mean that we should focus our students’ training on teaching skills and data science skills, especially when these are not our own areas of expertise. Excellent research training will be important for both industry positions and teaching-oriented faculty positions. But we should encourage our students to think about getting some significant training in teaching and/or data science, which will be important even if they take positions in research-oriented universities. And we should encourage some of our students to take industry internships and get teaching experience. But mostly we should avoid sending the implicit or explicit message to our students that they are failures if they don’t pursue tenure-track research university positions. If, as a field, we increase the number of our PhDs who take positions outside of research universities, this will make life better for everyone

]]>In the example video, the coherence level is 25% on some trials and 50% on others (i.e., on average, 25% or 50% of the dots move in one direction, and the other dots move randomly). A line appears at the end of the trial to indicate the direction of motion for that trial. When you watch a given trial, try to guess the precise direction of motion. If you are like most people, you will find that you guess a direction that is approximately 180° away from the true direction on a substantial fraction of trials. You may even see the motion start in one direction and then reverse to the true direction. We recommend that you maximize the video and view it in HD.

In the controlled laboratory experiments described in our poster (which you can download here), we find that 180° errors are much more common than other errors. In addition, our studies suggest that this is a bona fide illusion, in which people confidently perceive a direction of motion that is the opposite of the true direction. If you know of any previous reports of this phenomenon, let us know!

]]>Evidence that people can suppress salient-but-irrelevant color singletons has come from ERP studies and from behavioral studies. The ERP studies find that, under appropriate conditions, singleton distractors will elicit a Pd component, a putative electrophysiological signature of suppression (discovered by Hickey, Di Lollo, and McDonald, 2009). The behavioral studies show that processing at the location of the singleton is suppressed below the level of nonsingleton distractors (reviewed by Gaspelin & Luck, 2018). Are these electrophysiological and behavioral signatures of suppression actually related?

In the present study, Nick Gaspelin and I used an experimental paradigm in which it was possible to assess both the ERP and behavioral measures of suppression. First, we were able to demonstrate that suppression of the salient singleton distractors was present according to both measures. Second, we found that these two measures were correlated: participants who should a larger Pd also showed greater behavioral suppression.

Correlations like these can be difficult to find (and believe). First, both the ERP and behavioral measures can be noisy, which attenuates the strength of the correlation and reduces power. Second, spurious correlations are easy to find when there are a lot of possible variables to correlate and relatively small Ns. A typical ERP session is about 3 hours, so it's difficult to have the kinds of Ns that one might like in a correlational study. To address these problems, we conducted two experiments. The first was not well powered to detect a correlation (in part because we had no idea how large the correlation would be, making it difficult to assess the power). We did find a correlation, but we were skeptical because of the small N. We then used the results of the first experiment to design a second experiment that was optimized and powered to detect the correlation, using an a priori analysis approach developed from the first experiment. This gave us much more confidence that the correlation was real.

We also included a third experiment that was suggested by the alway-thoughtful John McDonald. As you can see from the image above, the Pd component was quite early in Experiments 1 and 2. Some authors have argued that an early contralateral positivity of this nature is not actually the suppression-related Pd component but instead reflects an automatic salience detection process. To address this possibility, we simply made the salient singleton the target. If the early positivity reflects an automatic salience detection process, then it should be present whether the singleton is a distractor or a target. However, if it reflects a task-dependent suppression mechanism, then it should be eliminated when subjects are trying to focus attention onto the singleton. We found that most of this early positivity was eliminated when the singleton was the target. The very earliest part (before 150 ms) was still present when the singleton was the target, but most of the effect was present only when the singleton was a to-be-ignored distractor. In other words, the positivity was not driven by salience per se, but occurred primarily when the task required suppressing the singleton. This demonstrates very clearly that the suppression-related Pd component can appear as early as 150 ms when elicited by a highly salient (but irrelevant) singleton.

]]>In a previous blog post (and follow-up), I mentioned my graduate mentor's approach, which emphasized self-replication. In this post, I go back to my intellectual grandfather, Bob Galambos, whose discoveries you learned about as a child even if you didn't learn his name. I hope you find his advice useful. It's impractical in some areas of science, but it's what a lot of cognitive psychologists have done for decades and still do today (even though you can't easily tell from their journal articles). I previously wrote about this in the second edition of An Introduction to the Event-Related Potential Technique, and the following is an excerpt. I am "recycling" this previous text because the relevance of this story goes way beyond ERP research.

My graduate school mentor was Steve Hillyard, who inherited his lab from his own graduate school mentor, Bob Galambos (shown in the photo). Dr. G (as we often called him) was still quite active after he retired. He often came to our weekly lab meetings, and I had the opportunity to work on an experiment with him. He was an amazing scientist who made really fundamental contributions to neuroscience. For example, when he was a graduate student, he and fellow graduate student Donald Griffin provided the first convincing evidence that bats use echolocation to navigate. He was also the first person to recognize that glia are not just passive support cells (and this recognition essentially cost him his job at the time). You can read the details of his interesting life in his autobiography and in his NY Times obituary.

Bob was always a font of wisdom. My favorite quote from him is this: “You’ve got to get yourself a phenomenon” (he pronounced phenomenon in a slightly funny way, like “pheeeenahmenahn”). This short statement basically means that you need to start a program of research with a robust experimental effect that you can reliably measure. Once you’ve figured out the instrumentation, experimental design, and analytic strategy that allows you to reliably measure the effect, then you can start using it to answer interesting scientific questions. You can’t really answer any interesting questions about the mind or brain unless you have a “phenomenon” that provides an index of the process of interest. And unless you can figure out how to record this phenomenon in a robust and reliable manner, you will have a hard time making real progress. So, you need to find a nice phenomenon (like a new ERP component) and figure out the best ways to see that phenomenon clearly and reliably. Then you will be ready to do some real science!

]]>

However, when we use NHST, we instead know the probability that we will get a Type I error when the null hypothesis is true. In other words, when the null hypothesis is true, we have a 5% chance of finding p < .05. **But this 5% rate of false positives occurs only when the null hypothesis is actually true**. We don’t usually know that the null hypothesis is true, and if we knew it, we wouldn't bother doing the experiment and we wouldn’t need statistics.

In reality, we want to know the false positive rate (Type I error rate) in a mixture of experiments in which the null is sometimes true and sometimes false. In other words, we want to know how often the null is true when p < .05. In one of the examples shown in the previous post, this probability (FPRP) was about 9%, and in another it was 47%. These examples differed in terms of statistical power (i.e., the probability that a real effect will be significant) and the probability that the alternative hypothesis is true [p(H1)].

The table below (Table 2 from the original post) shows the example with a 47% false positive rate. In this example, we take a set of 1000 experiments in which the alternative hypothesis is true in only 10% of experiments and the statistical power is 0.5. The box in yellow shows the False Positive Report Probability (FPRP). This is the probability that, in the set of experiments where we get a significant effect (p < .05), the null hypothesis is actually true. In this example, we have a 47% FPRP. In other words, nearly half of our “significant” effects are completely bogus.

The point of this example is **not** that any individual researcher actually has a 47% false positive rate. The point is that NHST doesn’t actually guarantee that our false positive rate is 5% (even when we assume there is no p-hacking, etc.). The actual false positive rate is unknown in real research, and it might be quite high for some types of studies. As a result, it is difficult to see why we should ever care about p values or use NHST.

In this follow-up post, I’d like to address some comments/questions I’ve gotten over social media and from the grad students and postdocs in my lab. I hope this clarifies some key aspects of the previous post. Here I will focus on 4 issues:

What happens with other combinations of statistical power and p(H1)? Can we solve this problem by increasing our statistical power?

Why use examples with 1000 experiments?

What happens when power and p(H1) vary across experiments?

What should we do about this problem?

If you don’t have time to read the whole blog, here are four take-home messages:

Even when power is high, the false positive rate is still very high when H1 is unlikely to be true. We can't "power our way" out of this problem.

However, when power is high (e.g., .9) and the hypothesis being tested is reasonably plausible, the actual rate of false positives is around 5%, so NHST may be reasonable in this situation

In most studies, we’re either not in this situation or we don’t know whether we’re in this situation, so NHST is still problematic in practice

The more surprising an effect, the more important it is to replicate

My grad students and postdocs wanted to see the false positive rate for a broader set of conditions, so I made a little Excel spreadsheet (which you can download here). This spreadsheet can calculate the false positive rate (FPRP) for any combination of statistical power and p(H1). This spreadsheet also produces the following graph, which shows 100 different combinations of these two factors.

This figure shows the probability that you will falsely reject the null hypothesis (make a Type I error) given that you find a significant effect (p < .05) for a given combination of statistical power and likelihood that the alternative hypothesis is true. For example, if you look at the point where power = .5 and p(H1) = .1, you will see that the probability is .47. This is the example shown in the table above. Several interesting questions can be answered by looking at the pattern of false positive rates in this figure.

*Can we solve this problem by increasing our statistical power? *Take a look at the cases at the far right of the figure, where power = 1. Because power = 1, you have a 100% chance of finding a significant result if H1 is actually true. But even with 100% power, you have a fairly high chance of a Type I error if p(H1) is low. For example, if some of your experiments test really risky hypotheses, in which p(H1) is only 10%, you will have a false positive rate of over 30% in these experiments even if you have incredibly high power (e.g., because you have 1,000,000 participants in your study). The Type I error rate declines as power increases, so more power is a good thing. **But we can’t “power our way out of this problem” when the probability of H1 is low**.

*Is the FPRP ever <= .05? *The figure shows that we do have a false positive rate of <= .05 under some conditions. Specifically, when the alternative hypothesis is very likely to be true (e.g., p(H1) >= .9), our false positive rate is <= .05 no matter whether we have low or high power. When would p(H1) actually be this high? This might happen when your study includes a factor that is already known to have an effect (usually combined with some other factor). For example, imagine that you want to know if the Stroop effect is bigger in Group A than in Group B. This could be examined in a 2 x 2 design, with factors of Stroop compatibility (compatible versus incompatible) and Group (A versus B). p(H1) for the main effect of Stroop compatibility is nearly 1.0. In other words, this effect has been so consistently observed that you can be nearly certain that it is present in your experiment (whether or not it is actually statistically significant). [H1 for this effect could be false if you’ve made a programming error or created an unusual compatibility manipulation, so p(H1) might be only 0.98 instead of 1.0.] Because p(H1) is so high, it is incredibly unlikely that H1 is false and that you nonetheless found a significant main effect of compatibility (which is what it means to have a false positive in this context). Cases where p(H1) is very high are not usually interesting — you don’t do an experiment like this to see if there is a Stroop effect; you do it to see if this effect differs across groups.

A more interesting case is when H1 is moderately likely to be true (e.g., p(H1) = .5) and our power is high (e.g., .9). In this case, our false positive rate is pretty close to .05. This is good news for NHST: **As long as we are testing hypotheses that are reasonably plausible, and our power is high, our false positive rate is only around 5%.**

This is the “sweet spot” for using NHST. And this probably characterizes a lot of research in some areas of psychology and neuroscience. Perhaps this is why the rate of replication for experiments in cognitive psychology is fairly reasonable (especially given that real effects may fail to replicate for a variety of reasons). Of course, the problem is that we can only guess the power of a given experiment and we really don’t know the probability that the alternative hypothesis is true. This makes it difficult for us to use NHST to control the probability that our statistically significant effects are bogus (null). In other words, **although NHST works well for this particular situation, we never know whether we’re actually in this situation**.

The example shown in Table 2 may seem odd, because it shows what we would expect in a set of 1000 experiments. Why talk about 1000 experiments? Why not talk about what happens with a single experiment? Similarly, the Figure shows "probabilities" of false positives, but a hypothesis is either right or wrong. Why talk about probabilities?

The answer to these questions is that p values are useful only in telling you the long-run likelihood of making a Type I error in a large set of experiments. ** P values do not represent the probability of a Type I error in a given experiment.** (This point has been made many times before, but it's worth repeating.)

NHST is a heuristic that aims to minimize the proportion of experiments in which we make a Type I error (falsely reject the null hypothesis). So, the only way to talk about p values is to talk about what happens in a large set of experiments. This can be the set of experiments that are submitted to a given journal, the set of experiments that use a particular method, the set of experiments that you run in your lifetime, the set of experiments you read about in a particular journal, the set of experiments on a given topic, etc. For any of these classes of studies, NHST is designed to give us a heuristic for minimizing the proportion of false positives (Type I errors) across a large number of experiments. My examples use 1000 experiments simply because this is a reasonably large, round number.

We’d like the probability of a Type I error in any given set of experiments to be ~5%, but this is not what NHST actually gives us. **NHST guarantees a 5% error rate only in the experiments in which the null hypothesis is actually true.** But this is not what we want to know. We want to know how often we’ll have a false positive across a set of experiments in which the null is sometimes true and sometimes false. And we mainly care about our error rate when we find a significant effect (because these are the effects that, in reality, we will be able to publish). In other words, we want to know the probability that the null hypothesis is true in the set of experiments in which we get a significant effect [which we can represent as a conditional probability: p(null | significant effect); this is the FPRP]. Instead, NHST gives us the probability that we will get a significant effect when the null is true [p(significant effect | null)]. These seem like they’re very similar, but the example above shows that they can be wildly different. In this example, the probability that we care about [p(null | significant effect)] is .47, whereas the probability that NHST gives us [p(significant effect | null)] is .05**.**

For each of the individual points shown in the figure above, we have a fixed and known statistical power along with a fixed and known probability that the alternative hypothesis is true (p(H1). However, we don’t actually know these values in real research. We might have a guess about statistical power (but only a guess because power calculations require knowing the true effect size, which we never know with any certainty). We don’t usually have any basis (other than intuition) for knowing the probability that the alternative hypothesis is true in a given set of experiments. So, why should we care about examples with a specific level of power and a specific p(H1)?

Here’s one reason: Without knowing these, we can’t know the actual probability of a false positive (the FPRP, p(null is true | significant effect)). As a result, unless you know your power and p(H1), you don’t know what false positive rate to expect. And if you don’t know what false positive rate to expect, what’s the point of using NHST? So, if you find it strange that we are assuming a specific power and p(H1) in these examples, then you should find it strange that we regularly use NHST (because NHST doesn’t tell us the actual false positive rate unless we know these things).

The purpose of examples like the one shown above is that they can tell you what might happen for specific classes of experiments. For example, when you see a paper in which the result seems counterintuitive (i.e., unlikely to be true given everything you know), this experiment falls into a class in which p(H1) is low and the probability of a false positive is therefore high. And if you can see that the data are noisy, then the study probably has low power, and this also tends to increase the probability of a false positive. So, even though you never know the actual power and p(H1), you can probably make reasonable guesses in some cases.

Most real research consists of a mixture of different power levels and p(H1) levels. This makes it even harder to know the effective false positive rate, which is one more reason to be skeptical of NHST.

I ended the previous post with the advice that my graduate advisor, Steve Hillyard, liked to give: Replication is the best statistic. Here’s something else he told me on multiple occasions: The more important a result is, the more important it is for you to replicate it before publishing it. Given the false positive rates shown in the figure above, I would like to rephrase this as: The more surprising a result is, the more important it is to replicate the result before believing it.

In practice, a result can be surprising for at least two different reasons. First, it can be surprising because the effect is unlikely to be true. In other words, p(H1) is low. A widely discussed example of this is the hypothesis that people have extrasensory perception.

However, a result can also seem surprising because it’s hard to believe that our methods are sensitive enough to detect it. This is essentially saying that the power is low. For example, consider the hypothesis that breast-fed babies grow up to have higher IQs than bottle-fed babies. Personally, I think this hypothesis is likely to be true. However, the effect is likely to be small, there are many other factors that affect IQ, and there are many potential confounds that would need to be ruled out. As a result, it seems unlikely that this effect could be detected in a well-controlled study with a realistic number of participants.

For both of these classes of surprising results (i.e., low p(H1) and low power), the false positive rate is high. So, when a statistically significant result seems surprising for either reason, you shouldn’t believe it until you see a replication (and preferably a preregistered replication). Replications are easy in some areas of research, and you should expect to see replications reported within a given paper in these areas (but see this blog post by Uli Schimmackfor reasons to be skeptical when the p value for every replication is barely below .05). Replications are much more difficult in other areas, but you should still be cautious about surprising or low-powered results in those areas.

]]>This paper from last spring describes new evidence for our hyperfocusing theory of cognitive dysfunction in schizophrenia. Remarkably, we found that people with schizophrenia were actually better able to focus centrally and filter peripheral distractors than were control subjects. Under the right conditions, we even observed a (slightly) larger P3 wave in patients than in controls.

This new papers shows that visual short-term memory guides attention in infants. Whereas adults orient toward items matching the contents of VSTM, infants orient toward non-matching items.

]]>There has been a lot written over the past decade (and even longer) about problems associated with null hypothesis statistical testing (NHST) and p values. Personally, I have found most of these arguments unconvincing. However, one of the problems with p values has been gnawing at me for the past couple years, and it has finally gotten to the point that I'm thinking about abandoning p values. Note: this has nothing to do with p-hacking (which is a huge but separate issue).

Here's the problem in a nutshell: If you run 1000 experiments over the course of your career, and you get a significant effect (p < .05) in 95 of those experiments, you might expect that 5% of these 95 significant effects would be false positives. However, as an example shown later in this blog will show, **the actual false positive rate may be 47%**, even if you're not doing anything wrong (p-hacking, etc.). In other words, nearly half of your significant effects may be false positives, leading you to draw completely bogus conclusions that you are able to publish. On the other hand, your false positive rate might instead be 3%. Or 20%. And my false positive rate might be very different from your false positive rate, even though we are both using p < .05 as our criterion for significance (even if neither of us is engaged in p-hacking, etc.). In other words,** p values do not actually tell you anything meaningful about the false positive rate**.

But isn't this exactly what p values are supposed to tell us? Don't they tell us the false positive rate? Not if you define "false positive rate" in a way that is actually useful. Here's why:

The false positive rate (Type I error rate) as defined by NHST is the probability that you will falsely reject the null hypothesis when the null hypothesis is true. In other words, if you reject the null hypothesis when p < .05, this guarantees that you will get a significant (but bogus) effect in only 5% of experiments in which the null hypothesis is true. However, this is a statement about what happens when the null hypothesis is actually true. In real research, we don't know whether the null hypothesis is actually true. If we knew that, we wouldn't need any statistics! In real research, we have a p value, and we want to know whether we should accept or reject the null hypothesis. The probability of a false positive in that situation is not the same as the probability of a false positive when the null hypothesis is true. It can be way higher.

For example, imagine that I am a journal editor, and I accept papers when the studies are well designed, well executed, and statistically significant (p < .05 without any p-hacking). I would like to believe that no more than 5% of these effects are actually Type I errors (false positives). In other words: I want to know the probability that the null is true given that an observed effect is significant. We can call this probability "p(null | significant effect)". However, what NHST actually tells me is the probability that I will get a significant effect if the null is true. We can call this probability "p(significant effect | null)". These two probabilities seem pretty similar, because they have the exactly the same terms (but in opposite orders). Despite the superficial similarity, in practice they can be vastly different.

The rest of this blog provides concrete examples of how these two probabilities can be very different and how the probability of a false positive can be much higher than 5%. These examples involve a little bit of math (just multiplication and division — no algebra and certainly no calculus). But you can't avoid a little bit of math if you want to understand what p values can and cannot tell you. If you've never gone through one of these examples before, it's well worth the small amount of effort needed. It will change your understanding of p values.

The first example simulates a simple situation in which—because it is a simulation—I can make assumptions that I couldn't make in actual research. These assumptions let us see exactly what would happen under a set of simple, known conditions. The simulation, which is summarized in Table 1, shows what I would expect to find if I ran 1000 experiments in which two things are assumed to be true: 1) the null and alternative hypotheses are equally likely to be true (i.e., the probability that there really is an effect is .5); 2) when an effect is present, there is a 50% chance that it will be statistically significant (i.e., my power to detect an effect is .5). These two assumptions are somewhat arbitrary, but they are a reasonable approximation of a lot of studies.

Table 1 shows what I would expect to find in this situation. The null will be true in 500 of my 1000 experiments (as a result of assumption 1). In those 500 experiments, I would expect a significant effect 5% of the time (assuming that my alpha is .05). This is because my Type I error rate is 5% (assuming an alpha of .05). This Type I error rate is what I previously called p(significant effect | null), because it's the probability that I will get a significant effect when the null hypothesis is actually true. In the other 500 experiments, the alternative hypothesis is true. Because my power to detect an effect is .5 (as a result of assumption 2), I get a significant effect in half of these 500 experiments. Unless you are running a lot of subjects in your experiments, this is a pretty typical level of statistical power.

However, the Type I error rate of 5% does not help me determine the likelihood that I am falsely rejecting the null hypothesis when I get a significant effect, p(null | significant effect). This probability is shown in the yellow box. In other words, in real research, I don't actually know when the null is actually true or false; all I know is whether the p value is < .05. This example shows that—if the null is true in half of my experiments and my power is .05—I would expect to get 275 significant effects (i.e., 275 experiments in which p < .05), and I would expect that the null is actually true in 25 of these 275 experiments. In other words, the probability that one of my significant effects is actually bogus (a false positive) is 9%, not 5%.

This might not seem so bad. I'm still drawing the right conclusion over 90% of the time when I get a significant effect (assuming that I've done everything appropriately in running and analyzing my experiments). However, there are many cases where I am testing bold, risky hypotheses—that is, hypotheses that are unlikely to be true. As Table 2 shows, if there is a true effect in only 10% of the experiments I run, almost half of my significant effects will be bogus (i.e., p(null | significant effect) = .47).

The probability of a bogus effect is also high if I run an experiment with low power. For example, if the null and alternative are equally likely to be true (as in Table 1), but my power to detect an effect (when an effect is present) is only .1, fully 1/3 of my significant effects would be expected to be bogus (i.e., p(null | significant effect) = .33).

Of course, the research from most labs (and the papers submitted to most journals) consist of a mixture of high-risk and low-risk studies and a mixture of different levels of statistical power. But without knowing the probability of the null and the statistical power, I can't know what proportion of the significant results are likely to be bogus. This is why, as I stated earlier,** p values do not actually tell you anything meaningful about the false positive rate**. In a real experiment, you do not know when the null is true and when it is false, and a p value only tells you about what will happen when the null is true. It does not tell you the probability that a significant effect is bogus. This is why I've lost my faith in p values. They just don't tell me anything.

Yesterday, one of my postdocs showed me a small but statistically significant effect that seemed unlikely to be true. That is, if he had asked me how likely this effect was before I saw the result, I would have said something like 20%. And the power to detect this effect, if real, was pretty small, maybe .25. So I told him that I didn't believe the result, even though it was significant, because p(null | significant effect) is high when an effect is unlikely and when power is low. He agreed.

Tables 1 and 2 make me wonder why anyone ever thought that we should use p values as a heuristic to avoid publishing a lot of effects that are actually bogus. The whole point of NHST is supposedly to maintain a low probability of false positives. However, this would require knowing p(null | significant effect), which is something we can never know in real research. We can see what would be expected by conducting simulations (like those in Tables 1 and 2). However, we do not know the probability that the null hypothesis is true (assumption 1) and we do not know the statistical power (assumption 2), and we would need to know these to be able to calculate p(null | significant effect). So why did statisticians tell us that we should use this approach? And why did we believe them? [Moreover, why did they not insist that we do a correction for multiple comparison when we do a factorial ANOVA that produces multiple p values? See this post on the Virtual ERP Boot Camp blog and this related paper from the Wagenmakers lab.]

Here's an even more pressing, practical question: What should we do given that p values can't tell us what we actually need to know? I've spent the last year exploring Bayes factors as an alternative. I've had a really interesting interchange with advocates of Bayesian approaches about this on Facebook (see the series of posts beginning on April 7, 2018). This interchange has convinced me that Bayes factors are potentially useful. However, they don't really solve the problem of wanting to know the probability that an effect is actually null. This isn't what Bayes factors are for: this would be using a Bayesian statistic to ask a frequentist question.

Another solution is to make sure that statistical power is high by testing larger sample sizes. I'm definitely in favor of greater power, and the typical N in my lab is about twice as high now as it was 15 years ago. But this doesn't solve the problem, because the false positive rate is still high when you are testing bold, novel hypotheses. The fundamental problem is that p values don't mean what we "need" them to mean, that is p(null | significant effect).

Many researchers are now arguing that we should, more generally, move away from using statistics to make all-or-none decisions and instead use them for "estimation". In other words, instead of asking whether an effect is null or not, we should ask how big the effect is likely to be given the data. However, at the end of the day, editors need to make an all-or-none decision about whether to publish a paper, and if we do not have an agreed-upon standard of evidence, it would be very easy for people's theoretical biases to impact decisions about whether a paper should be published (even more than they already do). But I'm starting to warm up to the idea that we should focus more on estimation than on all-or-none decisions about the null hypothesis.

I've come to the conclusion that best solution, at least in my areas of research, is what I was told many times by my graduate advisor, Steve Hillyard: "Replication is the best statistic." Some have argued that replication can also be problematic. However, most of these potential problems are relatively minor in my areas of research. And the major research findings in these areas have held up pretty well over time, even in registered replications.

I would like to end by noting that lots of people have discussed this issue before, and there are some great papers talking about this problem. The most famous is Ionnidis (2005, PLoS Medicine). A neuroscience-specific example is Button et al. (2015, Nature Reviews Neuroscience) (but see Nord et al., 2017, Journal of Neuroscience for an important re-analysis). However, I often find that these papers are bombastic and/or hard to understand. I hope that this post helps more people understand why p values are so problematic.

For more, see this follow-up post.

]]>I read this article—a review of the then-new feature integration theory—early in my first year of grad school. It totally changed my life. My first real experiment in grad school was an ERP version of the "circles and lollies" experiment shown in the attached image:

Luck, S. J., & Hillyard, S. A. (1990). Electrophysiological evidence for parallel and serial processing during visual search. Perception & Psychophysics, 48, 603-617.

In that experiment, I discovered the N2pc component (because I followed some smart advice from Steve Hillyard about including event codes that indicated whether the target was in the left or right visual field). I've ended up publishing dozens of N2pc papers over the years (along with at least 100 N2pc papers by other labs).

The theory presented in this Scientific American paper was also one of the inspirations for my first study of visual working memory:

Luck, S. J., & Vogel, E. K. (1997). The capacity of visual working memory for features and conjunctions. Nature, 390, 279-281.

As you may know, Anne passed away recently (see NY Times obituary). Anne was my most important scientific role model (other than my official mentors). I'm sure she had no idea how much impact she had on me. She probably thought that I was an idiot, because I became a blathering fool anytime I was in her presence (even after I had moved on from grad student to new assistant professor and then to senior faculty). But her intelligence and creativity just turned me to jello...

Anyway, this is a great paper, and very easy to read. I recommend it to anyone who is interested in visual cognition.

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In this recent TICS paper, Nick Gaspelin and I review the growing evidence that the human brain can actively suppress objects that might otherwise capture our attention.

]]>Bae, G. Y., & Luck, S. J. (2018). Dissociable Decoding of Working Memory and Spatial Attention from EEG Oscillations and Sustained Potentials. The Journal of Neuroscience, 38, 409-422.

In this recent paper, we show that it is possible to decode the exact orientation of a stimulus as it is being held in working memory from sustained (CDA-like) ERPs. A key finding is that we could decode both the orientation and the location of the attended stimulus with these sustained ERPs, whereas alpha-band EEG signals contained information only about the location.

Our decoding accuracy is only about 50% above the chance level, but it's still pretty amazing that such precise information can be decoded from brain activity that we're recording from electrodes on the scalp!

Stay tuned for more cool EEG/ERP decoding results — we will be submitting a couple more studies in the near future.