Martijn Cremers is Professor of Finance at the University of Notre Dame; Erasmo Giambona is the Michael Falcone Chair in Real Estate at the Whitman School of Management at Syracuse University; Simone M. Sepe is Professor of Law and Finance at the College of Law at the University of Arizona; and Ye Wang is a PhD Candidate in the Department of Finance at Bocconi University. This post responds to a post, titled The Long-term Effects of Hedge Fund Activism: A Reply to Cremers, Giambona, Sepe, and Wang, by Lucian Bebchuk, Alon Brav, Wei Jiang, and Thomas Keusch (available on the Forum here). The post by Professors Bebchuk, Brav, Jiang and Keusch replied to the criticism of the study on The Long-Term Effects of Hedge Fund Activism by Lucian Bebchuk, Alon Brav, and Wei Jiang (discussed on the Forum here) that was put forward in a paper by Cremers, Giambona, Sepe and Wang discussed in this post.

In a December 10, 2015 post to the Harvard Corporate Governance Blog, Professors Lucian Bebchuk, Alon Brav, Wei Jiang, and Thomas Keusch (“BBJK”) suggest that a study the four of us have recently coauthored, Hedge Fund Activism and Long-Term Firm Value (the “CGSW study”), “overlooks prior opposing evidence on the subject, offers a flawed empirical analysis, and makes [contradictory] claims.” For these reasons—BBJK unequivocally conclude—the CGSW study’s claims “should be given no weight in the ongoing examination of hedge fund activism.” We are thankful to BBJK for the time spent analyzing our work and the occasion they have provided us to offer a few clarifications. Hopefully, those clarifications will add clarity to our attempt at better understanding the effects of hedge fund activism, which is what, ultimately, we should all care about.

For the benefit of those not already familiar with the BBJK post and the CGSW study and to prevent details from obscuring the main issues under discussion, let us first clarify what we think is the main contribution of our study as it currently stands. We are only focusing on the long-term performance of firms after they are targeted by hedge funds. We then show that we can replicate the main result of a prior study coauthored by three of the authors of the BBJK’s post, The Long-Term Effects of Hedge Fund Activism, which was recently published in the Columbia Law Review (the “LT Effects Study”). The LT Effects Study reports that firms targeted by activist hedge fund tend to improve in performance afterwards compared to before they were targeted. Our main empirical finding is that this improvement in the long-term performance of targeted firms appears on average to be weaker than the improvement in performance over the same period of similar “control” firms that were not targeted. This finding challenges the interpretation that the improvement in the long-term performance of targeted firms can be ascribed to the activist hedge fund campaign.

We thus think that the real substantive issue is whether we have chosen control firms that are indeed “similar” to the targeted firms—that is, whether we compared the long-term performance of firms targeted by hedge funds to the performance of non-targeted control firms in such a way that the control firms are actually similar to the targeted firms in dimensions that really matter.

Therefore, the three key questions are:

(1) What are the dimensions that matter for the probability of being targeted in an activist hedge fund campaign?
(2) How successful are different empirical methodologies in finding control firms that match the targeted firms on those dimensions?
(3) Using the most successful methodology to find control firms that match targeted firms on the dimensions that matter, how different is the performance of the targeted firms from the performance of the control firms?

As a side note, let us observe that even if one were fully convinced about the answers to each of the above questions, the interpretation of any difference in performance would still involve judgment informed by economic and legal-institutional theories. Nevertheless, it seems to us that the issues raised by BBJK do not concern such judgment, but rather are limited to three key questions we have identified above.

Let us briefly summarize here what BBJK assert regarding our answers to those questions, before discussing their specific comments. Regarding the first key question, it seems to us that BBJK do not object to the answer we provide in the CGSW study, namely that it is important to control for past performance when considering the performance of firms after these have been targeted. Regarding the second question, BBJK assert—but do not show—that we have been thoroughly unsuccessful, even though our comparison of targeted and control firms shows their similarity in what we think we all agree are critical dimensions, and even if we have tried several different matching approaches. We thus anxiously await BBJK’s announced implementation of a careful matching methodology, so that we can compare our approaches more productively. Our counter-assertion would be that the approach taken in the LT Effects Study is insufficient, as we have tried to document in the CGSW study. The third question, on the long-term performance after being targeted by hedge funds, can only be answered once and to the extent that the first two questions are settled.

One additional preliminary observation made by BBJK seems worth addressing before proceeding to the discussion of their specific comments. BBJK lament that our study exclusively focuses on Tobin’s Q—i.e., as they write, “financial economists’ standard metric of firm valuation”—omitting to consider stock returns. In response, we can anticipate that a forthcoming revised version of our study will offer an extended appendix that includes, among others, results on stock returns. Nonetheless, as opposed to Q, stock returns tend to be a very noisy measure of long-term firm value. This explains why Q tends to be preferred to stock returns as the standard metric of firm value in financial studies, as BBJK themselves recognize (and could further explain why all of the regressions in the LT Effects Study involving stock returns produce statistically insignificant results, which are hard to interpret).

Turning to BBJK’s main comments, we reply to each comment below, reporting the original comment in bold to make it easier to follow the specifics of our reply.

I. CGSW’s Data and Results

BBJK assert that they obtain different results than those reported by our study when applying our matching methodology. They also suggest that this may be due to a lack of clarity on our part in describing the matching procedure we employ. We are surprised that BBJK were not able to replicate what we have done. We use completely standard procedures to match each targeted firm to its closest control firm from the entire universe of COMPUSTAT firms. We use four different matching procedures with different covariates. Two procedures are based on nearest neighbor matching (using the nnmatch Stata command) and two on propensity score (using the pscore2 Stata command).

We also apologize for not giving a ius primae noctis to some of the authors of the BBJK’s post so that they could validate our paper. Our decision to post the paper on SSRN or to share it with others (with no fanfare on our part, though) before doing so showed a lack of sensitivity on our part.

II. Claims Inconsistent with CGSW’s Own Results

BBJK observe that the patterns displayed in Figure 1 of the CGSW study do not support our claim that firms targeted by activist hedge funds improve less in value relative to the group of control firms. However, this is only an apparent inconsistency. In Figure 1, we document the average univariate results based on our matched sample. However, observed associations of the dependent variable (Q) cannot be exclusively attributed to the independent variable of interest (hedge fund activism), but may depend on other firm characteristics (the control variables), such that we only draw conclusions from multivariate comparisons. Using multivariate regressions, we are able to better isolate the impact of hedge fund activism on Q. These percentage effects are reported in our Tables 5 and 6, which clearly show that the firms targeted by activist hedge funds perform worse than the matched group from year 1 to year 5 after the hedge fund intervention. Further, column (6) in these tables shows that the targeted and control firms have no observable differences in Q before the start of the campaigns (as indicated by the statistically insignificant coefficient on the interaction of (HF_Target × t-4 to t-1), see the CGSW study at 38-40 for further details).

III. The Puzzling “Discovery” of a Selection Effect

BBJK suggest that our claim about the existence of a selection issue affecting hedge fund activism is puzzling as it would be well-known that hedge funds tend to target poorly performing firms. This seems a partial reading of our claim, though. A more accurate reading of that claim would have specified it includes the following two prongs. First, since selections issues affect hedge fund activism—a point on which we all seem to agree—any association with subsequent performance needs to be examined with particular caution. Second, unlike approaches used in prior studies, matching offers an empirical procedure that can more convincingly mitigate any selectivity bias, if such matching is done in the “right” dimensions that matter for selection. In particular, we disagree that the approach used in the LT Effects Study cited by BBJK can be considered as a viable alternative to matching.

IV. Prior Matched Sample Analysis Reaching Opposite Conclusions

BBJK further observe that we do not consider prior studies that have employed matching procedures to examine the long-term impact of hedge fund activism. This is a comment that we particularly appreciate, as we recognize that the literature section of our paper is probably its most underdeveloped part. Of course, we are committed to substantially improve it in the next version of our study. Nonetheless, we make here a few preliminary observations on the papers BBJK suggest we should consider. First, we are not aware of, and BBJK do not refer to, any publicly available studies that are directly comparable to our setting, namely that focus on Q and match by lagged Q. As to the long-term study that BBJK presented at the American Law and Economics Association in May 2015, we anxiously await the unveiling of the written results of that paper. During its presentation in May 2015, one of us inquired about the paper’s matching procedures. He was told that the authors used several procedures but was not informed about the details, just that the results were robust. Therefore, it is unclear to us whether those procedures also include matching on predetermined Q, as we do in our paper.

V. Flaws in Empirical Analysis

BBJK emphatically point out that our matched sample analysis is flawed. The main reason on which they ground this claim is that “to get industry-adjusted Tobin’s Q, CGSW have chosen to compare the Tobin’s Q of each firm to the median in its 4-digit SIC industry, a large fraction of 4-digit SIC industry buckets have only 1 or 2 public firms in any given year, rendering the authors’ non-standard procedure for industry adjustment highly problematic.” As specified in the paper, however, we use several matching procedures that deliver different matching samples. Such samples include what we have termed “Alternative Matched Sample 1,” which uses Tobin’s Q rather than industry-adjusted Tobin’s Q and our results are on average stronger (see CGSW at 15,18). BBJK then add that there are additional substantial methodological concerns about our matching procedure, but they put off the discussion of those concerns to a future research paper.

VI. Inconsistency with the Large Body of Evidence on Stock Returns

BBJK also claim that there would be an inconsistency between the short-term gains associated to hedge fund interventions and the loss in long-term value experienced by targeted firms. We do not see that inconsistency. As we showed in the CGSW study, the Q of firms targeted by hedge funds increases in absolute terms after the hedge fund intervention. The problem is that the targets perform worse than the control firms in the matched sample, i.e., firms sharing similar characteristics to the targets but which experience no hedge fund intervention. This story seems perfectly compatible with hedge fund intervention being individually rewarding (i.e., the fund gets a position when the target’s value is X>0 and it resells the position when its value is X+Y, with Y>0), but socially inefficient (i.e., firms with the same value X at the time of the hedge fund intervention but which are not targeted by the fund have a long-term value of X+Z, with Z>Y). The difference Z-Y is the magnitude of the social inefficiency we claim hedge fund intervention produces over time.

VII. Implausible Claims

We understand the concern of BBJK as to the results we obtained on innovative firms. However, we also suspect that there might be a misunderstanding about the kind of economic significance we refer to in our study, and will give more discussion in our revision. The reported three-year decline in value exceeding 50% for targeted innovative firms is calculated relative to, among other things, the performance of innovative firms that were not targeted, the Q of which increased substantially over this period.

* * *

Our paper highlights that prior evidence on the consequences of hedge fund intervention is not conclusive. We hope our findings will stimulate researchers to study the economic, legal, and institutional channels through which hedge fund activism affects shareholders value. Finally, we again want to thank BBJK for their feedback, which we hope to incorporate in the next revision of our paper and which we think will substantially improve our study.

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