Unilateral Effects Analysis in Differentiated Product Markets: Guidelines, Policy, and Change

This Cournot-based unilateral effects model is not discussed further in this paper, because it focuses on homogeneous goods.

The hypothetical monopolist test posits the thought-experiment of a single firm that sells a group of similar products and suggests that a relevant market exists when that firm can profitably impose a small, but significant and non-transitory increase in price (SSNIP). In principle, this approach could lead to a duopoly market structure whenever a merger enables a SSNIP. However, the 2010 Merger Guidelines mandate that closer substitutes must be in the same market (Merger Guidelines 2010, sec 4.1.1). A similar argument could mandate the inclusion of all products with the potential to reposition into closer substitutes. (Alternatively, firms with the potential to supply a product that is comparable to the merged firm would also be considered rivals in the narrow market based on supply-side considerations.) The 2010 Guidelines also note that the analysis need not start with market definition, because evidence of competitive effects could itself be useful in proving a market. On its face, the 1992 Guidelines took a different approach by starting with market definition. The approaches were only modestly different, however, because the iterative style of the 1992 Merger Guidelines allowed evidence that is uncovered during the investigation to substantiate further a market definition analysis.

The reference to a 35 % market share (Merger Guidelines 1992, sec 2.211) ties back to the dominant firm model that was noted in the 1982 Guidelines and serves as a limit on unilateral effects enforcement. The 2010 Guidelines relax this limit but substitute an implicit expectation to show some direct effects evidence that is suggestive of a likely anticompetitive effect in weak structural cases.

Farrell and Shapiro’s (2010) “upward pressure on price” (UPP) analysis represents one empirical implementation of this concept. UPP analysis assumes the price effects of a merger depend on the internalization of the merger’s change in market structure as both firms adjust their pricing to reflect the effect of those price changes on the profits of the merger partner. In effect, the “cost” of a price increases falls, because some of the lost sales are recaptured by the merger partner.

For example, repositioning would negate the effect if the third-closest rival could reposition its product and eliminate the loss of competition from the merger. If the second and third alternatives were very similar, this repositioning could be easy.

The 2010 Merger Guidelines also mention sufficiency of entry; however, the repositioning analysis customizes the sufficiency analysis to the conditions that are faced by existing rivals, and therefore the sufficiency analysis in the entry section may not be relevant. In order to preclude the finding of a unilateral effect, repositioning by significant rivals must be sufficient to deter or defeat the potential unilateral concern.

For a given product, conclusions on differentiation can vary. Economists are more likely to see product differentiation, while attorneys are more likely to find commonalities that make the product relatively homogeneous. The products themselves can be physically differentiated and yet be considered homogeneous as long as versions of them can competitively meet the needs of specific customers. In Sect. 3, the data analysis will use the attorney classification, as that choice has the most significant effect on policy (because the attorneys are expected to litigate the case, their choices are constrained by a combination of the case law, the Guidelines, and the pricing behavior).

The horizontal merger investigation data report (FTC 2013) reviewed all HSR mergers that were filed between fiscal years 1996 and 2011 to collect information on market structure. Due to the time limitations that are implicit in the HSR process, the FTC may not collect specific information on every serious competitive overlap between the merging parties in every merger investigation. In effect, two merger regimes were explored in the report: one in which market-specific information was used to supplement the specific structural details on the relevant market; and another in which industry-specific generalizations were used in place of the market-specific data. In any particular case, the depth of the investigation depended on issues such as: the number of markets that were closely reviewed in a merger; the type of industry; staffing availability; the likely outcome of the investigation; and historical experience with the market. Limiting the analysis to mergers having one to three relevant markets allowed the project to focus on staff reviews that use industry-specific data.

As was noted in footnote 8, the study collected more extensive information from a restricted sample of mergers, in which the staff closely studied the expected anticompetitive effects in the one-to-three markets that were affected by the merger. This subsample covered 70 % of the horizontal mergers in the full review. The restricted one-to-three sample included: oil markets (6 %); pharmaceutical markets (17 %); chemical markets (10 %); and grocery retailing markets (6 %). Looking at the investigations in the sample of all (1992–2012) mergers that were fully reviewed by the FTC, one would find 7 % oil mergers, 15 % pharmacy mergers, 11 % chemical mergers, and 5 % grocery retailing mergers. Thus, the restricted sample of markets generally reflected the full sample of mergers reviewed by the FTC (The markets reviewed by the Agency skew towards oil (20 %) and grocery (12 %) because mergers in those markets often generate large numbers of local concerns. An econometric policy analysis that is based on the universe of markets would bias the policy review towards the standard that is applied in the over-represented oil and grocery retailing industries). The actual 176-market sample differs from the universe of FTC mergers because it focuses on relatively differentiated products by design. Of course, this sample does not represent the universe of mergers, because it excludes those that were reviewed by the Department of Justice (DOJ). The DOJ data are not available, so no analysis is possible.

In mergers to monopoly, the merging parties are found to be the closest rivals and hold the ability unilaterally to impose a SSNIP. Interview, documentary, or analytical evidence serves to substantiate the high diversion level that is implied by the closest rival concept, while other evidence shows that more distant rivals are not able to influence their behavior. In other markets, the merging parties may be identified as closest competitors but will face other rivals that limit their market behavior.

A Commission finding on unilateral effects was also inferred when an anticompetitive unilateral theory was clearly identified by the staff analysis, but the investigation closed due to sufficient evidence on ease of entry or other procompetitive considerations.

By construction, low diversion requires both diversion ratios to be considered to be low; while a finding of head-to-head competition could be limited to one firm (a high diversion ratio from one merger partner to another would tend to trigger a competitive concern).

Shapiro’s (1996) model adjusts the diversion ratio for sales that are lost to competitive alternatives outside the market. We lack the required data and do not implement this adjustment. Approximately 20 of the 176 markets offered the potential for the estimation of a structural demand system. These analyses were not undertaken in all of the 20, because: (1) the procedure was rarely used early in the sample; (2) time constraints; or (3) modeling issues. When a demand system was estimated, the price effect was simulated directly, thereby bypassing diversion analysis. Alternative forms of merger simulation are a more recent introduction and thus rarely appear in the 20-year sample (hospital mergers represent an exception with numerous examples after 2006).

Testing shows the effects of the timeliness and likelihood effects do not differ; thus, considering the evidence to be substitutable is reasonable.

This approach classifies 174 of the 176 observations in the sample (with only nine values decreased to one, and one value increased to negative one). Both types of effects were observed in the two remaining observations. For one observation, the evidence findings seemed to cancel out, and thus the variable was set to zero. For the other observation, two considerations implied a competitive problem, while only one factor pointed to continued competition. For this observation, a value of one was assigned, under the assumption that the weight of the evidence for that observation pointed to a competitive problem.

This approach would be questionable if each evidence variable had a different effect on the finding of a unilateral effect. The next section tests for this possibility; it is not found to be a problem.

In a few situations, approximations were required to recover the market share data from the facts presented in the memo. When required, the companion review by the Bureau of Economics is also used.

See Coate and Fischer (2014) for the details. In that paper, 51 markets were identified by the prominence of price as the controlling competitive variable. In 27 of the markets, direct price competition appeared relevant, while in another 24 markets, price was relevant via a bargaining market. In 41 markets, dynamic competition was relevant, with 13 markets focused on innovation and 28 on other forms of competition.

In some of these markets, product quality serves as the key avenue of competition. For other products, it is the competition to define or promote a specific product that leads to sales. Price is a secondary characteristic, set as part of a customized marketing strategy.

Both variables are subject to logarithmic transformations to address their likely non-linear effects. A one was added to the fringe share data, to avoid taking the log of zero.

Sample selection is always a concern in modeling policy decisions. However, here it is possible to argue that the selection affects either weak or strong cases, and due to the probit estimation structure, is unlikely to affect the model’s accuracy. To elaborate: Some mergers are withdrawn, because the agency is very likely to find a unilateral effect (e.g., three-to-two mergers are regularly seen as causing unilateral effects in differentiated product markets). Other mergers are cleared without a second request (hence, they are excluded from the data set). Our sample cannot include these; hence, our model may not directly apply to such markets (the population of markets we model explicitly excludes cases that were withdrawn or cleared without a full “second-request” review). However, any bias in our model’s ability to predict such (excluded) markets is likely to be quite small. This is because the predictions for very strong or weak markets are likely to be very close to one or zero, respectively, when predicted with our model. In other words, a merger that is not proposed because it is very likely to create anticompetitive unilateral effects would be predicted by our model to have a probability of the Commission’s finding a unilateral violation that is very close to one. A merger that is cleared without a second request would tend to be predicted by our model to have a nearly zero probability for a finding of a unilateral violation.

Chi-square statistic of 18.5 is greater than the critical level of 15.5 with nine degrees of freedom. As Allison (1999) notes, tests for differences between parameters are meaningless if the latent variance in a probit or logit model differs across groups; he proposes a test for this possibility. Thus, throughout this paper, in any instance where we split a pool to test for separate coefficients according to some group (e.g., in this regression, according to Price Competition), we implemented Allison’s test for difference in the latent variance, using Glenn Hoetker’s complogit Stata procedure (see Hoetker (2007), for description). In no instance did we find a difference in the variances of the latent variables. When there is no difference in the latent variance, Allison suggests continuing with conventional methods for comparing coefficients; we thus proceed to test the coefficients with the Chi-square test. Note that Hoetker’s complogit procedure actually tests a logit model. However, the logit and probit models are very similar in form, and neither p value was smaller than 0.23 (the null is no difference), which suggests that there would be no difference had we implemented the test for a probit model.

Pooling populations in which some variables have different slopes may generate misleading results; see, e.g., Gujarati (1995, pp. 524–525).

The specification assumes that the treatment of a positive indication is the same as the treatment of a negative indication. This hypothesis was tested and could not be rejected (Chi-square test statistic = 0.93).

We also tested if there was a difference in the impact of “strong” versus “very strong” barriers to repositioning. In this regression, we included a third indicator for “very strong” evidence, which was equal to one when staff of both the Bureau of Competition and Economics agreed that both timeliness and likelihood impediments to entry existed or agreed that one impediments existed and differ on the other finding. This coefficient was insignificantly different from zero (t-statistic = −0.91) in the price regression, suggesting that finding more than two impediments has the same impact as finding of two.

By definition, Type I error has a 10 % probability of occurring (with a 10 % significance level) in any given hypothesis test. For example, applying the binomial distribution to a situation of ten (independent) hypothesis tests generates a probability of obtaining at least one Type I error of 65 % (this binomial distribution example is not directly applicable to our models, since our estimated coefficients are not independent, but it illustrates the point).

Technically, it is impossible to calculate the elasticity for a binary variable, because a percentage increase in a binary variable is undefined. We thus start by calculating the marginal coefficients for the binary variables (see, e.g., the Stata manual, section titled “margins,” available at www.​stata.​com/​manuals13/​rmargins.​pdf). To make these numbers comparable to elasticities, we extrapolate this change to predict the hypothetical change in outcome that is associated with a 1 % increase in the binary variable from its mean. That is, we multiply this change in outcome by the 0.01 times the mean of the binary variable. Dividing this result by the predicted outcome at the means of the explanatory variable gives the relevant value. This approach is not dissimilar to the partial elasticity suggested by Greene and Hensher (2010). The partial elasticity can be recovered by dividing our elasticities by the mean of the binary variable.

Findings of head-to-head competition materially increase the likelihood of a unilateral effects finding in both price and non-price models, while findings of distant rivalry lower the probability of a unilateral effect to trivial levels. Thus, not every comparison yields prediction differences.

Comparing outcomes with hypothetical or “adjusted” outcomes has a long history in the labor economics literature (see, Altonji and Blank 1999) and has been recently applied in comparing merger enforcement policies (e.g., Bergman et al. 2010; Szücs 2012).

Each of the 176 observations is associated with a fitted probability that is defined by the data and coefficients in Column 1 of Table 3. The adjustment process to treat price markets as non-price simply replaces the “1” value of Price Competition with a zero for each price observation in the dataset, keeping the value of the other variables as they actually are. A comparable calculation treats non-price markets as price by changing the “0” value of Price Competition to “1” for all non-price markets.

There are two ways to predict this number: either directly calculating the relevant percentage or using the model to predict the likelihood of a unilateral effects finding for each market and then averaging those predictions. The two are asymptotically equivalent. We use the latter method, because it made the bootstrap method of obtaining the standard errors in Table 4 simpler to implement.

For the pooled model, the t-statistics represent the significance test for the coefficient of the price variables. For the split model, the t-statistics are obtained from bootstrapping, using Stata’s nldecompose command, as described in Sinning et al. (2008) [the difference between actual and hypothetical rates is the difference that is due to coefficients in the Oaxaca (1973) decomposition].

T-statistics for Table 5 are also bootstrapped. Stata’s nldecompose procedure is not equipped to handle this model, so we custom-wrote a simple procedure for this table. This bootstrapped t-test retains the standard one-tail hypothesis test.

One test for a policy shift after the issuance of the Commentary on the Horizontal Merger Guidelines (2006) and another test for a policy shift that might be associated with Republican administrations were both run and no significant results generated. A time trend was also introduced into the equation, again with no significant results (t-statistics = 1.18, −0.94, for the price and non-price regressions, respectively).

For a discussion on the importance of facts in unilateral effects analysis, see Timothy Muris, “Antitrust Enforcement at the Federal Trade Commission: In a Word-Continuity” speech to American Bar Association Antitrust Section, August 7, 2001 at points II-B and II-D. Available at http://​www.​ftc.​gov/​public-statements/​2001/​08/​antitrust-enforcement-federal-trade-commission-word-continuity.

Unlike the Muris regime, no change was observed in the non-price model; hence, that equation is not shown.