What doesn't kill you makes you stronger: Psychological trauma and its relationship to enhanced memory control.

Experiment 1

In Experiment 1, we defined the lower- and higher-trauma groups based on a postexperimentally administered traumatic experiences survey ( Goldberg & Freyd, 2006 ). The survey asked participants to estimate the frequency of a range of traumatic incidents (e.g., witnessing or experiencing accidents, natural disasters, violence, sexual assault/abuse, emotional abuse, and the death of significant individuals) separately for the periods before age 18 and afterward. We divided our sample into equal groups reporting lower and higher levels of total trauma events prior to the age of 18, while holding our stimulus and test order counterbalancing factors constant. We sought to establish two groups that were treated identically during the experiment, notwithstanding their differing levels of self-reported trauma. If a greater history of trauma provides a natural opportunity to practice retrieval suppression, and if these experiences yield a generalized suppression skill, we should find greater suppression-induced forgetting in our higher-trauma group.

Participants were undergraduates ( N = 48) receiving credit for a course requirement. The stopping point for data collection was preselected based on previous research using a similar design ( Anderson & Green, 2001 ) and was constrained by counterbalancing (there were 24 unique cells after combining our stimulus and test order counterbalancing factors; see Materials). An additional five participants were run but were excluded and will not be considered further on the basis of their inability to reach criterion for initial learning ( n = 2), failure to comply with instructions ( n = 2), or history of brain damage ( n = 1). These exclusion criteria were based on long-standing lab protocols (see, e.g., Anderson et al., 2004 , 2011 ) and supported by empirical evidence (e.g., Hertel & Calcaterra, 2005 ). All participants provided written informed consent in accordance with the protocol approved by the University of Oregon’s Institutional Review Board.

Traumatic experiences survey

We administered the Brief Betrayal-Trauma Survey (BBTS; Goldberg & Freyd, 2006 ) after participants completed the TNT task. The 12-item survey asked participants to estimate the frequency of traumatic incidents separately for the periods before age 18 and afterward. Because the mean age of participants in Experiment 1 was only 20.35 years ( SD = 2.21), we operationalized trauma history as the average frequency score based on events that happened before age 18, disregarding type of trauma. Specifically, these average scores were derived from participants’ best estimate of the number of instances of each type of trauma assessed using a 6-point scale for each item on the survey [0 = never ; 1 = one time ; 2 = two to five times ; 3 = six to 20 times ; 4 = 21 to 100 times ; 5 = more than 100 times ]. See Table S1 in the online supplemental materials for descriptive statistics and further demographic information.

Procedure

Participants initially viewed each of the word pairs for 6 s. After this study phase, we drilled participants on the pairs. We presented each cue and asked participants to vocally respond with the associated response word within a 4-s time window. We provided corrective feedback after each trial. We gave participants up to three cycles to correctly recall at least 50% of the items, a training threshold representative of many studies (e.g., Anderson & Green, 2001 ; Anderson et al., 2004 ; Benoit & Anderson, 2012 ; van Schie & Anderson, 2017 ).

After reaching learning criterion, participants entered the TNT phase, in which we instructed them to say the associated response word to any cue word presented in green as fast as possible (feedback would be presented if they failed to respond out loud). In contrast to these Think trials, if a cue word appeared in red (indicating a No-Think trial), they were to avoid both thinking about and saying the response word for the same 4-s trial duration. In all cases, participants were to direct their eyes and attention to the cue word. Cue words appeared consistently in either green or red 0 (Baseline), 1, or 16 times during the phase. The counterbalancing of word pairs across these six conditions (0, 1, or 16 repetitions in either the Think or No-Think instruction conditions) crossed with the two possible response pairings described earlier (neutral and negative valence), produced 12 counterbalancing cells to achieve full balancing of stimulus materials across conditions.

Two surprise recall tests were then administered for all of the learned responses ( Anderson & Green, 2001 ). The same probe (SP) test presented participants with the original cue words, for which they had up to 4 s to say the associated response aloud. The independent probe (IP) test was structured similarly, except that the probe consisted of a novel semantic cue and a word stem. The two tests were administered in a counterbalanced order across participants. Combining this test order factor with the 12 stimulus-counterbalancing levels discussed above yielded a total of 24 unique counterbalancing combinations. For both the SP and IP tests, we encouraged participants to provide the correct answer as quickly as possible for every probe, regardless of the instructions during the TNT phase.

After the final memory tests, participants rated each word from the stimulus set and a random selection of 30 positive words in terms of valence using a method akin to the ANEW ( Bradley & Lang, 1999 ). A postexperimental questionnaire assessing compliance was then administered prior to the Beck Depression Inventory (see Table S1 for BDI scores; Beck, Steer, & Carbin, 1988 ). Finally, we asked participants to complete Goldberg and Freyd’s (2006) traumatic experiences survey, which was used to establish their group status. Given that 24 participants were required to obtain even counterbalancing, we ran 48 participants, to enable construction of two groups, matched perfectly for counterbalancing, but differing in reported trauma.

Analysis approach

In analyzing the final test recall data, we first examined suppression-induced forgetting and retrieval-induced facilitation effects across test types (i.e., aggregated over the SP and IP tests) to characterize the general influence of our instruction manipulation on recall, irrespective of the nature of the final test cue. We then followed these analyses with tests of possible interactions by test type to determine whether the effects of interest generalized over different retrieval cues used to assess performance. If suppression-induced forgetting is cue-independent, for example, we would expect it to emerge in response to both types of test cues. If a significant interaction with test type was observed, we characterized these effects separately for each test type to isolate the nature of the interaction. If an overall effect was significant but no interaction observed, we interpreted this to suggest that test type did not moderate the overall effect, consistent with cue-independence.

We analyzed the relation between trauma experience and inhibitory control over memory via a group analysis (see later section entitled “Integrated Analyses of Experiments 1 and 2” for a complementary analysis using robust correlation). We divided our sample into equal groups reporting lower and higher levels of trauma, while holding our stimulus and test order counterbalancing factors constant. Thus, lower- and higher-trauma groups were established via a median split based on participants’ trauma scores, separately within each of our 24 counterbalancing conditions. By combining the lower-trauma halves of each of these splits together, we formed a fully counterbalanced sample that had lower trauma scores than did the corresponding higher-trauma group, which was similarly composed by combining the higher-trauma halves of these splits (for other examples of this approach, see, e.g., Anderson et al., 2004 ; Hanslmayr, Leipold, Pastötter, & Bäuml, 2009 ). In cases for which participants had the same trauma frequency (of which there were two), ties were broken based on the number of traumas reported after the age of 18 or, in a single case, a coin toss. 1

One disadvantage of our group analysis approach is that it runs the risk of reducing the difference in level of trauma across the higher- and lower-trauma groups. By conducting the median split within each counterbalancing group, for example, it is possible for the “higher” trauma participants in one split to have lower levels of trauma than “lower” trauma groups in a different split for another counterbalancing group. Thus, by insisting on the constraint that the groups be matched across all counterbalancing dimensions, the trauma scores of the two groups may have some overlap. To determine whether this issue compromised how strongly our lower- and higher-trauma groups differed in their level of trauma, we conducted a check on the quality of our split. To do this, we compared the trauma levels in our carefully matched median split to the trauma levels that would have been obtained had we simply performed a median split on the entire sample of 48, disregarding counterbalancing. This latter version of the split revealed a difference in average trauma scores across the groups that broadly matched that of the groups formed using the original procedure (compare Table S1 with Table S2), suggesting that our matching procedure did little to compromise how strongly the higher- and lower-trauma groups differed.

Final test phase performance

By crossing the instruction factor (Think vs. No-Think) with repetition (0 vs. 16), our experiment had two identical Baseline (0 repetitions) cells. Because these cells should not meaningfully differ, we combined them for ANOVAs that focused on the suppression-induced forgetting and retrieval-induced facilitation effects. The ANOVA addressing the overall memory control effect (Think vs. No-Think), however, necessitated separation of these baselines (e.g., testing the interaction of repetition by instruction). 2

Overall memory control effects

Participants showed robust control over the retrieval process, as reflected by the interaction of instruction with repetition on final test recall, F (1, 24) = 20.86, p < .001, η p 2 = .465. Both lower-trauma participants, F (1, 24) = 3.17, p = .088, η p 2 = .117, and higher-trauma participants, F (1, 24) = 21.90, p < .001, η p 2 = .477, showed evidence for control effects, as can be seen in Figure 1 . This recall benefit for Think items relative to No-Think items indicates that participants could, at a minimum, stop the retrieval process from occurring on No-Think trials often enough to preempt the strengthening/facilitation that retrieved Think items usually exhibit. It does not, however, address the separate effects of retrieval-induced facilitation (specifically, Think recall relative to Baseline) or suppression-induced forgetting (specifically, No-Think recall relative to Baseline), which we discuss next.

Final test results by trauma group in Experiment 1. The top panels present aggregate final recall (averaged across same-probe [SP] and independent-probe [IP] measures) scores relative to Baseline performance for Think and No-Think items as a function of repetition. Being repeatedly exposed to reminders facilitated Think items in a way not observed for No-Think items in either trauma group. Yet, only the higher-trauma group (top right panel) exhibited significant below-Baseline forgetting of No-Think items as a result of retrieval suppression. The bottom panel depicts suppression-induced forgetting (16 No-Think repetitions – 0 repetition Baseline) separately on SP and IP tests of forgetting. Negative values represent suppression-induced forgetting as a result of previous suppression attempts, whereas positive values represent suppression-induced facilitation. Error bars reflect SE s.

Retrieval-induced facilitation

Consistent with prior work, we found that final recall performance for Think items was reliably better after 16 retrieval attempts than after none (Baseline), F (1, 24) = 61.79, p < .001, η p 2 = .720. This effect did not interact with valence, F < 1. Importantly, the facilitation did not differ reliably across trauma groups, F < 1, despite a small numerical tendency for higher-trauma participants to show less facilitation. Thus, attending to Think items produced retention benefits that were statistically similar for the two trauma groups. This similarity of facilitation across higher- and lower-trauma groups was true irrespective of target item valence, as reflected in a nonsignificant trauma History × Repetition × Valence (neutral vs. negative) interaction, F < 1.

Facilitation was, however, greater when Think items were tested on the SP compared with the IP test, F (1, 24) = 85.10, p < .001, η p 2 = .780. In particular, whereas the SP test showed robust facilitation of Think items, F (1, 24) = 151.45, p < .001, η p 2 = .863, the IP test showed no evidence of facilitation, F < 1. This attenuated facilitation on the IP test is consistently observed in the Think/No-Think paradigm (see Anderson & Huddleston, 2011 , for a meta-analysis of 1300 participants tested with IPs) and indicates that the benefits of repeated retrieval on later retention are primarily associative and cue-specific.

Suppression-induced forgetting

Next, we examined whether suppressing the retrieval process impaired final test performance for No-Think items relative to Baseline performance. To estimate suppression, we compared recall of No-Think response words after 0 suppression attempts (Baseline) to performance after 16 suppression attempts. We first tested for suppression-induced forgetting, collapsed over type of test and valence, to assess the effect of suppression on overall retention. The group, as a whole, showed better recall in the Baseline condition than after retrieval suppression, although this effect was marginally significant, F (1, 24) = 4.06, p = .055, η p 2 = .145. Thus, independent of trauma history, suppressing retrieval tended to impair overall retention of suppressed items in a manner largely consistent with prior work. The counterbalanced order in which the two constituent tests were administered did not affect this conclusion, as reflected in a nonsignificant interaction of test Order × Repetition, F (1, 48) = 1.47, p = .232, η p 2 = .030. Importantly, the repetition effect did not interact with the emotional valence of the suppression target, F < 1, indicating that the effect was comparable for both neutral and negative items.

Of key interest, however, was whether participants who reported having lived through more traumatic experiences differed in how well they contended with unwanted memories. Strikingly, we found that, whereas participants with greater experience with trauma displayed significant forgetting of No-Think items (Baseline minus No-Think recall = 80% − 72%, yielding an 8% suppression-induced forgetting effect), F (1, 24) = 9.62, p = .005, η p 2 = .286, the lower-trauma group displayed no reliable evidence of this ability to forget, (Baseline minus No-Think recall = 77% − 77%, yielding a 0% effect), F < 1. This difference in suppression-induced forgetting was significant, as reflected by an interaction of repetition and trauma, F (1, 24) = 5.62, p = .026, η p 2 = .190. Importantly, this apparent trauma-history advantage did not interact reliably with the emotional valence of the target material being suppressed, F < 1, suggesting that it reflects a generalized skill of suppression, regardless of valence. Thus, more extensive trauma exposure was associated with an enhanced ability to suppress unwanted memories.